acceptodds
Under review as a conference paper at ICLR 2027

Logical Equivariance in Diffusion Language Models

Abstract

Rewriting a problem without changing its answer can change whether a language model solves it, even when average accuracy barely moves. We study this as logical equivariance: predictions should transform consistently with answer-preserving input changes. In four diffusion language models, paired evaluations on Sudoku, code, and mathematics reveal many problems solved in one presentation but not another. We build a Sudoku benchmark whose forced targets transport exactly under rotations and reflections, and prove that exact grid equivariance leaves row-major relative-score attention only two or three offset classes, so stability must be learned. In post-training, Reasoning-State Masking (RSM) improves solving but alone reduces stability; presentation randomization (PR) removes this cost, and its gain in normalized reliability is 8.3 points larger with RSM. Matched controls reproduce this interaction at two scales and trace its stability gain to training on partial states at RSM's density. The combined recipe raises LLaDA-8B's all-view correctness from 47.7% to 86.1% alongside higher accuracy, and improves worst-view maze success by 7.3–18.8 points.

Primary area:
generative models
Keywords:
Diffusion Language Models, Logical Equivariance, Structured Reasoning, Positional Encodings

Reviews

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

This paper studies an interesting and practical problem: if we rewrite a problem in an equivalent way (rotate a sudoku, swap two independent code lines, rename variables in a math question), the answer should not change, but diffusion LLMs often get it right in one form and wrong in another. They call this logical equivariance. They build a Sudoku benchmark where the targets are logically forced, so the answer transports exactly under rotations and reflections. They also evaluate code infilling and MATH-500 with paired transformations. Then they prove a theorem that row-major relative-score attention can only be exactly D4-equivariant if the offsets collapse into 2 or 3 classes. They propose a post-training recipe, RSM + PR, to get a better performance.

Critical strengths
  1. The evaluation idea for dllm is good. Tracking each problem across all its views and reporting ANY/ALL makes clear something average accuracy hides. Eq. 4 is simple but convincing to me.

  2. The Sudoku-AC-orbit construction is good. Keeping only states where the target cells are forced avoids the question of whether the answer really stays the same after the transformation.

Critical weaknesses
  1. The data used to train RSM is not clearly decribed. I think the data has some changes between experiments. In 5.4, "RSM uses the 4.6k puzzles for which the deduction procedure produces a trajectory, yielding 41k intermediate states." and in appendix, "The cache contains 67,551 states from 9,995 of 10,000 puzzles". I didn't get the difference. And I also found the comparsion is not 100% fair, see next point.

  2. RSM uses 4.6k trajectories, but canonical uses all. And also, the mask density is also different. It's good to have appednix C. But the contrast between A and C is a negative result if I understand it correctly, which means RSM doesn't work that well.

  3. Since AR models are still the mainstream, I think it's important to mention or set some AR models as baseline. Prompt-order and format sensitivity is well known in AR models (for example this paper: Multidimensional Consistency Improves Reasoning in Language Models), so without this comparison I cannot see what is specific to diffusion.

Questions for authors

From the weakness, I would like to ask:

  1. Why is the RSM training data different between Section 5.4 (4.6k puzzles, 41k states) and Appendix C (9,995 puzzles, 67,551 states)? Is the state generator different?

  2. How do you explain the negative result in Appendix C?

  3. Maybe some AR models could be included?

2 comments
AuthorsOpenReview ↗

Response to Reviewer ByqZ (1/2)

We thank the reviewer for the careful reading and for the positive view of the evaluation idea and the Sudoku-AC-Orbit construction. We address each weakness and question below with exact numbers and new experiments.

(Table numbers in this response refer to the original submission. In the revised PDF: original Table 2 → Table 1; Table 4 and Table 8 → Table 11; Table 15 → Table 23; Tables 17–18 → Tables 26–27. New results: decoding controls in Table 7 and Table 24, three-seed recipes in Tables 3 and 14–15, matched factorial in Table 28, token calibration in Table 29, refresh intervention in Table 30, matched mazes in Table 22, AR baselines in Tables 8–9, inference baselines in Table 10.)


W1 / Q1. One generator, two retention rules.

UseRetention rulePuzzlesStates
Table 4Trajectories that reach the completed board4,63341,135
AdditionalValid trajectories that stop before completion5,36226,416
Appendix CBoth9,99567,551

Five of the 10,000 puzzles emit no state. We'll added this table to the revision to clarify the data split.

W2. The comparison the review calls unfair is not the one our claim rests on. Appendix C exists to remove exactly the confounds you list, and we have now closed the last one.

  • Same data: Every arm uses the same 9,995 puzzles with the same frequencies.
  • Same density: Each random state hides as many cells as the paired reasoning state.
  • Same supervision per target: With hh hidden cells out of NN blanks, weighting a uniform random hidden set by NωiN \omega_i gives an expected coefficient of (h/N)(Nωi/h)=ωi(h/N)(N \omega_i/h) = \omega_i for every target. A new canonical arm completes this weight-matched 2×2 setup.

With all three matched, the RSM × PR interaction in mean success is +1.51 [1.04, 1.98] at 50M (5/5 seeds) and +2.45 [1.89, 3.01] at 100M (3/3 seeds). The interaction in sECR is +4.06 [2.61, 5.56] at 50M and +6.32 [4.70, 7.92] at 100M. Data amount, mask density, and target allocation do not explain this effect.

Q2. A vs C is not evidence that RSM fails. It is half of the result.

A vs C compares the two state types without PR. Reasoning states lower sECR by 4.36 points at 50M and 6.57 [5.18, 7.95] at 100M under matched weights. The other half is what happens with PR.

  • RSM+PR beats matched random+PR in solving. The gain is +0.94 [0.57, 1.29] on 50M Sudoku and +2.10 [1.58, 2.67] on 100M mazes (3 seeds, identical PR in both arms).
  • PR has opposite effects on the two state types. At 100M, the effect is −1.00 [−1.37, −0.64] on random states and +1.44 [0.84, 2.04] on reasoning states.
  • In the full recipe comparison with three training seeds, RSM+PR is first in mean success, estimated worst-view success, and sECR in every seed. Over the Canonical baseline, it gains +3.70 [3.19, 4.22], +3.39 [2.61, 4.16], and +2.77 [1.49, 4.04], respectively.
  • At 8B (Table 15 checkpoints, sampled same-input control), all-view correctness rises from 48.2% (Canonical) to 87.2% (RSM+PR), and the presentation-induced ANY − ALL gap falls from 51.6 to 12.8 points.

We also explain why A vs C is negative, and test the explanation.

  1. Theory. A fixed presentation per puzzle creates a puzzle-specific deviation from the orbit-averaged objective. Its gradient is mean-zero over presentation assignments, and reusing presentations in blocks adds exactly αC\alpha C to the gradient covariance. Fresh PR gives an unbiased gradient of the orbit-averaged objective.
  2. Measured before training. At the common pretrained checkpoint, in the last-two-blocks-plus-head projection, trC\text{tr} C is about 11× larger for reasoning states than for matched random states.
  3. Pre-specified intervention. Changing only how often presentations are re-drawn moves the sECR interaction progressively from 0.06 through 2.44 and 3.13 to 4.30 in separately trained models.
  4. Pre-specified control without a solver. Nested random trajectories give a smaller copy of the interaction (+1.74 [0.66, 2.90]).
  5. Independent measurement. In the 50M five-seed Appendix-C analysis, token leakage calibrated against a whole-output sampling reference shows the same interaction. The value is −0.00434 nats [−0.00547, −0.00322], and it remains negative in all 5 seeds.

Together, these results support presentation persistence as a mechanism for the state-dependent PR effect. The positive matched endpoints separately establish where the augmented reasoning-state model solves more.

AuthorsOpenReview ↗

Response to Reviewer ByqZ (2/2)

W3 / Q3. AR baselines: The phenomenon is shared.

We ran Qwen2.5-7B-Instruct and Llama-3.1-8B-Instruct with greedy decoding.

Sudoku orbits, 500 problems × 8 views:

ModelWindowMean successANYALLParse failures
Qwen2.5-7BAC457.5100.01.6663/4,000
Qwen2.5-7BAC166.742.60.0not tallied
Llama-3.1-8BAC227.487.00.025/4,000
Llama-3.1-8BAC413.263.80.0not tallied

An AR model that solves 57.5% of views solves all eight views of a puzzle 1.6% of the time. Parsing does not explain this. For Llama AC2, at least 410/500 puzzles have all eight outputs parsed and still mix correct and incorrect answers. For Qwen AC4, at least 148/500 puzzles contain both a parsed-correct and a parsed-incorrect view.

MATH pairs, greedy (582 original–transformed pairs from 328 base problems; accuracy / ANY / ALL at the pair level, as in Table 2):

ModelAccuracyANYALLANY − ALL
Qwen2.5-7B (AR)36.041.630.411.2
Llama-3.1-8B (AR)31.739.024.414.6
LLaDA-8B (diffusion, Table 2)29.038.719.419.3

Parsing failures (Qwen 25/910 inputs, Llama 10/910) are counted as incorrect. All three models change correctness under answer-preserving rewrites of the same problem.

What the AR baselines establish.

  1. Presentation dependence is not unique to diffusion. Prompt sensitivity in AR models is well known (e.g., Multidimensional Consistency Improves Reasoning in Language Models, now cited). What was missing is an exact test with targets that provably transport across presentations, ensuring disagreements are true errors rather than ambiguities. Our construction supplies this test, and it applies directly to AR models.
  2. Flexible generation order is not a solution. Arbitrary-order generation might seem like a natural defense against layout variations. Table 2 shows it is not. Generation order and input presentation are different axes.
  3. Masked diffusion enables our controlled intervention. Its explicit training distribution over partial states allows us to vary practiced conditional tasks while strictly matching data, mask density, and per-target supervision. Under this control at 100M, the identical PR augmentation lowers mean success on random states (−1.00) but raises it on reasoning states (+1.44).
  4. Architectural scope. The rigidity theorem assumes full, unmasked attention. This matches the masked-diffusion architecture, which is where we claim and test the structural result.
Reviewer_ZRTZOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper studies how logical equivariance affects a model's performance. Logical equivalence is defined for multiple domains such that the modifications to the input do not alter the final answer. The key hypothesis is that a model's prediction should be consistent under such modifications. The authors introduce Sudoku-AC-Orbit, which extends existing Sudoku dataset with such logical equivalence. Additionally, they also consider Math and code equivalence. They demonstrate that existing masked diffusion LMs are not consistent and further propose two post-training approaches, Reasoning-State Masking and presentation randomization, both of which are complementary in improving the model's consistency.

Critical strengths

The hypothesis is strong, well validated to be lacking in current diffusion LMs, and the proposed solutions are shown to be working on novel settings. Its an interesting finding that supervising on solver states without augmentation increases view dependence. This demonstrates the need for augmentation in the first place.

Critical weaknesses

My primary concern is with the novelty relative to prior work. PR is a fairly standard augmentation technique. Also, simple inference-time baselines such as majority voting, verify-and-select, etc. are not explored which are cheap techniques compared to training.

The large-model results in Table 2 could be due to sampling noise, and that is not mentioned / tested. If the decoding is stochastic (i.e., temperature used), the results need to be recomputed for a same-view re-decode baseline.

Questions for authors

NA

2 comments
AuthorsOpenReview ↗

Response to Reviewer ZRTZ (1/2)

We thank the reviewer for the positive assessment and for recognizing the finding that supervising solver states without augmentation increases view dependence. We address each weakness below with new experiments.

(Table numbers in this response refer to the original submission. In the revised PDF: original Table 2 → Table 1; Table 4 and Table 8 → Table 11; Table 15 → Table 23; Tables 17–18 → Tables 26–27. New results: decoding controls in Table 7 and Table 24, three-seed recipes in Tables 3 and 14–15, matched factorial in Table 28, token calibration in Table 29, refresh intervention in Table 30, matched mazes in Table 22, AR baselines in Tables 8–9, inference baselines in Table 10.)


W1a. The novelty is a new role of PR: removing a bias that state selection creates.

PR is usually treated as generic augmentation whose benefit does not depend on what the model is trained on. We show that this is false and explain why. When training states are selected per problem, as RSM does, and each problem is shown in a fixed presentation, the gradient carries a persistent, presentation-specific bias. Fresh PR removes it. PR's effect is therefore set by the supervised states:

  • Opposite signs. Under full matching (same puzzles, mask density, and per-target supervision), at 100M PR lowers mean success on random states by 1.00 [0.64, 1.37] points and raises it on reasoning states by 1.44 [0.84, 2.04]. The interaction is +2.45 [1.89, 3.01] (3/3 seeds), and +1.51 [1.04, 1.98] at 50M (5/5 seeds).
  • A measured learning-signal quantity. At a common pretrained checkpoint, presentation reuse contributes a covariance component; in the last-two-blocks-plus-head projection its trace is about 11× larger for reasoning states. Fresh PR removes this reuse component in the fixed-parameter analysis, not all gradient noise.
  • Verified by intervention. Separately trained models that differ only in how often presentations are re-drawn give interactions of 0.06 → 2.44 → 3.13 → 4.30 sECR, as pre-specified.
  • Replicated. In Table 4 with three training seeds, RSM+PR is first in mean, estimated worst-view, and sECR in every seed; the interaction is +7.63 [5.94, 9.32] sECR. The finding you highlighted (solver states without augmentation increase view dependence) holds in every seed: sECR 38.97 for RSM against 44.38 for Canonical.

PR has been understood as a way to add invariance through more varied data. Our results show that when training states are curated, it is also what removes the bias that curation introduces so the two must be designed together. With the forced-target orbit construction and the two/three-class theorem, this gives an evaluation, a structural result, and a controlled learning result, well beyond proposing an augmentation.

W1b. Training-recipe differences persist under equal-budget inference.

Same procedure and budget on every Table 4 checkpoint; mean success / joint success (all 8 views correct).

RecipeNative, 1 callRandom D4, 1 callCell-wise vote, 8 callsVerify-and-select, 8 calls
Canonical42.9 / 7.042.1 / 5.839.5 / 18.491.6 / 68.2
PR42.3 / 6.641.4 / 6.237.7 / 16.291.1 / 65.2
RSM46.3 / 7.444.5 / 7.842.5 / 16.691.7 / 73.8
RSM+PR46.8 / 7.646.3 / 8.444.3 / 19.292.0 / 72.6
  1. Voting hurts. Cell-wise majority voting lowers mean success for every recipe.
  2. Uniform random-view decoding is a legitimate symmetrization baseline. It preserves population orbit-mean success in expectation and symmetrizes the output law. It can change joint or worst-view behavior even though it does not add mean competence.
  3. Verify-and-select is strong, and recipe differences remain under the same 8-call procedure. RSM+PR exceeds Canonical by +4.40 [1.20, 7.60] and PR by +7.40 [4.00, 11.00] in joint success. RSM itself has the highest point estimate (73.8), so we report the full table rather than claiming one universally best recipe.
  4. Verify-and-select assumes a valid task-specific checker, which we provide here. At one native call, RSM+PR exceeds Canonical by +3.93 [2.68, 5.18] and PR by +4.48 [3.18, 5.78].

Our claim is that training-recipe differences persist in native solving and under fixed inference procedures.

AuthorsOpenReview ↗

Response to Reviewer ZRTZ (2/2)

W2. Table 2 is not sampling noise.

Table 2 uses greedy decoding, so no temperature is involved and a same-view re-decode reproduces the output. Every recorded flip in Table 2 is therefore caused by the change of presentation.

We also ran the same-view re-decode baseline you describe, under sampling. For each problem with m equivalent presentations (m = 8 for Sudoku, m = 2 for code and MATH), we compare m independent decodes of the original presentation (pseudo-orbit) with one decode of each of the m presentations (real orbit). Calls and decoder settings are identical. Both contain the same sampling noise, so a view-invariant model would show the same ANY − ALL gap in both. Values below are ALL / ANY (gap = ANY − ALL), in %.

TaskModelSame-view re-decodesDifferent presentationsGap increase
Sudoku AC16LLaDA-8B36.2 / 52.0 (15.8)1.3 / 98.6 (97.3)+81.5
Sudoku AC24LLaDA-8B11.4 / 22.4 (11.0)0.0 / 73.5 (73.5)+62.5
Sudoku AC32LLaDA-8B1.4 / 6.2 (4.8)0.0 / 26.6 (26.6)+21.8
Sudoku AC24Dream-7B75.0 / 89.8 (14.8)50.5 / 100.0 (49.5)+34.7
Sudoku AC32Dream-7B55.1 / 74.4 (19.3)17.4 / 99.9 (82.6)+63.2
Sudoku AC32iLLaDA-8B71.8 / 75.4 (3.6)23.0 / 99.0 (76.0)+72.4
Sudoku AC32LLaDA-MoE48.6 / 68.6 (20.0)6.3 / 99.8 (93.5)+73.5
CodeLLaDA-8B37.3 / 53.6 (16.3)28.5 / 57.6 (29.1)+12.8
CodeDream-7B40.9 / 59.3 (18.4)29.3 / 62.7 (33.4)+15.0
CodeiLLaDA-8B21.7 / 36.0 (14.3)15.3 / 43.2 (27.9)+13.6
CodeLLaDA-MoE33.6 / 59.0 (25.4)25.8 / 60.7 (34.9)+9.5
MATH-500LLaDA-8B16.8 / 29.4 (12.5)16.2 / 33.7 (17.5)+5.0
MATH-500Dream-7B14.3 / 17.5 (3.3)9.1 / 19.2 (10.1)+6.8
MATH-500iLLaDA-8B†17.3 / 30.5 (13.2)14.2 / 30.5 (16.3)+3.1
MATH-500LLaDA-MoE18.7 / 39.5 (20.8)17.5 / 42.1 (24.6)+3.8

Sudoku and code use T = 0.5. MATH uses T = 0.2, since Dream-7B's outputs collapse to empty strings at T = 0.5. †200 of 582 pairs. The full set will be added to the final version.

In every one of the 15 settings, the gap is larger across presentations than across re-decodes of the same presentation: by 22–82pp on Sudoku and 10–15pp on code, in every model, and by 3–7pp on MATH. Since both settings contain the same sampling noise, this additional gap is attributable to presentation. The same control on the fine-tuned 8B checkpoints of Table 15 gives same-view gaps of 0.0–0.2pp and cross-view gaps from 51.6pp (canonical SFT) down to 12.8pp (RSM+PR).

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

The authors of this paper show that diffusion models can solve problems in one form and then fail after a rewrite that preserves the answer. Examples would be rotating a Sudoku grid or renaming math variables in a problem. The authors also argue that average accuracy as a metric hides the problem. The authors have constructed an exact Sudoku benchmark that measures the consistency and show that row-major attention cannot guarantee grid symmetry on its own. Training on the intermediate reasoning states plus a random equivalent view fixes much of the problem. Overall it takes LLaDA-8B's correctness from 47.7% to 86.1%.

Critical strengths
  1. The benchmark is very solid. The forced-target Sudoku orbits guarantee that every view is truly the same problem with the same answer, giving a clean, reusable test of presentation consistency.

  2. The serialization rigidity theorem cleanly proves that row-major relative-position attention can only be exactly grid-equivariant if its offsets collapse to two or three classes. That is an explanation for why standard architectures can’t guarantee this symmetry.

Critical weaknesses
  1. The large-model ANY vs. ALL gaps (99% vs. 12.9–23.8%) use one prediction per view. Under stochastic decoding, much of this gap arises without any presentation dependence. The pseudo-orbit control is never applied to the large models, code, or math. Where it is applied, the excess spread is only 1.24 points.

  2. In Appendix C, density-matched random states plus PR match RSM plus PR in normalized reliability. RSM adds about one point of mean success at 50M and nothing resolved at 100M. The “interaction” mostly reflects RSM hurting stability on its own. Additionally, the supplementary code provided is lacking the RSM method so I am unable to check the core claims of this paper. Also there may be a mismatch in what PR means in the code vs the paper.

  3. The 50M study, 8B result, and maze results each come from one run; the maze settings are checkpoints from one pretraining trajectory. Seed variance is unknown, despite small key differences.

Minor Thing: The authors have cited many preprints from arxiv. Which is completely fine, this does not materially move this paper into reject or accept. However, several of these preprints have been accepted into publication. A good practice would be to use that particular citation.

Questions for authors

Was decoding for the large models (Table 2) greedy or sampled?

Can you report seed variance for the main comparisons? Even three seeds for the 50M recipe study (Table 4) and the key maze settings would show whether RSM+PR’s advantages exceed run-to-run noise.

Given Appendix C, what is RSM’s specific contribution?

Can you show a setting (harder puzzles, larger scale, maze) where reasoning-state structure clearly beats density-matched random states?

Can you release the RSM training code and confirm the PR configuration?

How were checkpoints selected in the main study and the 8B experiment?

3 comments
AuthorsOpenReview ↗

Response to Reviewer hMSt (1/3)

We thank the reviewer for the detailed review and for the positive view of the benchmark and the rigidity theorem. We address each weakness and question below with new experiments, including the seed repetitions and the matched maze study that the review requested.

(Table numbers in this response refer to the original submission. In the revised PDF: original Table 2 → Table 1; Table 4 and Table 8 → Table 11; Table 15 → Table 23; Tables 17–18 → Tables 26–27. New results: decoding controls in Table 7 and Table 24, three-seed recipes in Tables 3 and 14–15, matched factorial in Table 28, token calibration in Table 29, refresh intervention in Table 30, matched mazes in Table 22, AR baselines in Tables 8–9, inference baselines in Table 10.)


W1 / Q1. Table 2 is greedy, and the gap is not sampling noise.

Table 2 uses greedy decoding (temperature 0), so each prediction is the model's output for that view, not one draw from it. A view-invariant model decoded greedily has ANY = ALL.

As the reviewer suggests, we also applied the pseudo-orbit control to the large-model, code, and MATH evaluations. For each problem with m equivalent presentations (m = 8 for Sudoku, m = 2 for code and MATH), we compare the original presentation sampled m times (pseudo-orbit) with each of the m presentations sampled once (real orbit). Both contain the same sampling noise, so a view-invariant model would show the same ANY − ALL gap in both. Values below are ALL / ANY (gap = ANY − ALL), in %.

TaskModelPseudo-orbitReal orbitGap increase
Sudoku AC16LLaDA-8B36.2 / 52.0 (15.8)1.3 / 98.6 (97.3)+81.5
Sudoku AC24LLaDA-8B11.4 / 22.4 (11.0)0.0 / 73.5 (73.5)+62.5
Sudoku AC32LLaDA-8B1.4 / 6.2 (4.8)0.0 / 26.6 (26.6)+21.8
Sudoku AC24Dream-7B75.0 / 89.8 (14.8)50.5 / 100.0 (49.5)+34.7
Sudoku AC32Dream-7B55.1 / 74.4 (19.3)17.4 / 99.9 (82.6)+63.2
Sudoku AC32iLLaDA-8B71.8 / 75.4 (3.6)23.0 / 99.0 (76.0)+72.4
Sudoku AC32LLaDA-MoE48.6 / 68.6 (20.0)6.3 / 99.8 (93.5)+73.5
CodeLLaDA-8B37.3 / 53.6 (16.3)28.5 / 57.6 (29.1)+12.8
CodeDream-7B40.9 / 59.3 (18.4)29.3 / 62.7 (33.4)+15.0
CodeiLLaDA-8B21.7 / 36.0 (14.3)15.3 / 43.2 (27.9)+13.6
CodeLLaDA-MoE33.6 / 59.0 (25.4)25.8 / 60.7 (34.9)+9.5
MATH-500LLaDA-8B16.8 / 29.4 (12.5)16.2 / 33.7 (17.5)+5.0
MATH-500Dream-7B14.3 / 17.5 (3.3)9.1 / 19.2 (10.1)+6.8
MATH-500iLLaDA-8B†17.3 / 30.5 (13.2)14.2 / 30.5 (16.3)+3.1
MATH-500LLaDA-MoE18.7 / 39.5 (20.8)17.5 / 42.1 (24.6)+3.8

Sudoku and code use T = 0.5. MATH uses T = 0.2, since Dream-7B's outputs collapse to empty strings at T = 0.5. †200 of 582 pairs. The full set will be added to the final version.

In every one of the 15 settings, the gap is larger across presentations than when the same presentation is resampled: by 22–82pp on Sudoku and 10–15pp on code, in every model, and by 3–7pp on MATH. Since both settings contain the same sampling noise, this additional gap is attributable to presentation. The same control on the Table 15 checkpoints is reported with the 8B results below.

The 1.24-point figure is the pretrained row of Table 8. After post-training, the excess spread over pseudo-orbits is 11.11 for RSM and 4.05 for RSM+PR. Across three training seeds it is 11.78–12.35 and 4.41–4.84. We also add an exactly unbiased estimator of view dispersion, which needs no pseudo-orbit. Its interaction is positive at both scales (+0.00289 [0.00185, 0.00394] at 50M and +0.00440 [0.00338, 0.00548] at 100M).

AuthorsOpenReview ↗

Response to Reviewer hMSt (2/3)

W3 / Q2. Seeds for Table 4.

All four recipes, three fine-tuning seeds each from the same pretrained checkpoint, 9,000 updates, one evaluation harness (500 puzzles, 8 views, K = 16). Mean (between-seed SD):

RecipeMean successEstimated worst-view successsECR
Canonical42.81 (0.10)26.40 (0.16)44.38 (0.22)
PR41.68 (0.12)25.94 (0.11)44.94 (0.17)
RSM45.56 (0.04)25.56 (0.10)38.97 (0.17)
RSM+PR46.52 (0.05)29.79 (0.07)47.15 (0.08)
Contrast (crossed seed × puzzle 95% CI)Mean successEstimated worst-viewsECR
RSM+PR − Canonical+3.70 [3.19, 4.22]+3.39 [2.61, 4.16]+2.77 [1.49, 4.04]
RSM+PR − PR+4.84 [4.30, 5.40]+3.85 [3.10, 4.61]+2.21 [0.92, 3.49]
RSM × PR interaction+2.09 [1.52, 2.69]+4.69 [3.71, 5.71]+7.63 [5.94, 9.32]

RSM+PR is first on all three metrics in every seed. The interaction per seed is 1.95 / 2.34 / 1.98 (mean), 4.56 / 4.96 / 4.54 (estimated worst-view), 7.36 / 8.12 / 7.40 (sECR). Between-seed SDs are 0.04–0.22, while the contrasts are 2–8 points. The observed fine-tuning-seed variation does not explain these differences. The new table uses one common evaluator. Printed Table 4 values come from the original sampled run (e.g., RSM+PR 47.00 there and 46.48 for the same checkpoint here).

The matched studies add more independent seeds: 5 per arm at 50M (interaction 1.70, 1.65, 1.57, 1.46, 1.50), 3 at 100M, 3 per arm on mazes (+2.10 [1.58, 2.67], crossed interval).

8B. The Table 15 results use greedy decoding. To check that the 8B recipe differences are not a decoding artifact, we additionally evaluated the same checkpoints with the sampled pseudo-orbit control from W1 (T = 0.5, 8 samples per view). Values are ALL / ANY (gap), in %.

RecipePseudo-orbitReal orbitGap increase
Canonical SFT87.6 / 87.6 (0.0)48.2 / 99.8 (51.6)+51.6
PR89.4 / 89.4 (0.0)49.8 / 100.0 (50.2)+50.2
RSM94.4 / 94.6 (0.2)74.6 / 99.8 (25.2)+25.0
RSM+PR98.2 / 98.2 (0.0)87.2 / 100.0 (12.8)+12.8

Resampling the same presentation leaves correctness essentially unchanged for every recipe (pseudo-orbit gap 0.0–0.2pp), so the real-orbit gap is presentation-induced. The recipe ordering of Table 15 holds under sampling. RSM+PR narrows the presentation gap from 51.6pp to 12.8pp.

W2 / Q3. What RSM adds under matched controls: more solving, and a different PR effect. The normalized-retention endpoint contrast is unresolved (sECR −0.07 [−1.01, 0.83]). This is not evidence of equivalence. On absolute success, RSM+PR beats the matched random arm at 50M, and the factorial shows that PR's effect depends on the supervised states.

  1. RSM+PR solves more than matched random+PR. 50M: mean success +0.96 [0.62, 1.33] and estimated worst-view +0.66 [0.10, 1.22] (density-matched); +0.85 [0.52, 1.20] and +0.60 [0.04, 1.15] (target-weight-matched).
  2. The interaction is in accuracy, under full matching. +1.51 [1.04, 1.98] at 50M (5/5 seeds) and +2.45 [1.89, 3.01] at 100M (3/3). At 100M, PR changes mean success by −1.00 [−1.37, −0.64] on random states and by +1.44 [0.84, 2.04] on reasoning states.
  3. A pre-specified intervention tests the mechanism. At the common pretrained checkpoint, in the last-two-blocks-plus-head projection, the presentation-reuse covariance quantity is about 11× larger for reasoning states. Changing only how often a puzzle's view is re-drawn, in separately trained models, moves the interaction 0.06 → 2.44 → 3.13 → 4.30 sECR. Nested random trajectories without a solver give a smaller copy (+1.74 [0.66, 2.90]).

RSM chooses what the model conditions on. Matching each target's loss weight does not match the information visible next to it. This is consistent with the effect remaining under the matched controls.

AuthorsOpenReview ↗

Response to Reviewer hMSt (3/3)

Q4. Yes: mazes, and harder Sudoku.

RSM+PR minus matched random+PRMean success
Mazes 100M (same online PR, density, target weights; 3 seeds, 500 mazes)+2.10 [1.58, 2.67] (92.0 → 94.1)
Hardest Sudoku stratum, 272 puzzles the solver oracle cannot finish+1.22 [0.74, 1.72]; weight-matched +1.15 [0.67, 1.64]
Sudoku 50M, 5 seeds+0.94 [0.57, 1.29]
Sudoku 100M+0.32 [−0.03, 0.68]

The matched maze result establishes a solving gain, not a resolved normalized-stability gain. Maze sECR is +0.74 [−0.17, 1.63], unresolved. Separately, across the pre-specified Sudoku difficulty strata, the slope is +0.20 [−0.07, 0.48], also unresolved. We therefore do not claim that the gain increases monotonically with Sudoku difficulty.

Q5. RSM code and the exact PR configuration.

You are correct that the supplementary archive attached to the submission does not contain the RSM implementation. An earlier incomplete version of the code archive was inadvertently attached during submission. The revised supplementary material, now uploaded, contains the complete RSM state-generation and training code, with a README that maps each method to its command and gives the exact configurations for the Table 4 recipes, the matched Appendix C study, and the matched maze study.

We also audited the PR code to resolve the configuration question precisely. In the original Table 4 experiment, the PR branch uses the full_orbit_sft_10k recipe: the 10k base puzzles are expanded into all eight D4D_4 presentations, the resulting 80k examples are globally shuffled, and corruption is sampled independently after transformation for each example. RSM+PR uses the corresponding RSM state-orbit expansion. This is distinct from the separately reported PR grouped baseline, which groups the eight presentations of a puzzle and averages their losses.

The paper describes PR at the population-objective level as sampling g∼Unif(D4)g\sim\mathrm{Unif}(D_4). The full-orbit Table 4 implementation has the same uniform view marginal, but a different finite training schedule; the revised Appendix D.8 states this distinction.

For the matched Appendix-C experiment, all PR arms instead use the same online uniform-view procedure, eliminating PR implementation as an attribution confound. The same control was applied in the new matched maze experiment, where RSM+PR still improves mean success by +2.10 [1.58, 2.67] pp over matched random+PR.

Q6. Checkpoint selection. Table 4 and Appendix C: the final 9,000-update checkpoint, no selection. 8B: 8,000 steps; every 500 steps, 200 validation puzzles are decoded greedily and the checkpoint with the highest exact-match validation accuracy is kept.

Citations are updated to published versions.

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Paper summary

This paper studies logical equivariance of diffusion language models under answer-preserving transformations. It introduces a Sudoku evaluation with exactly transported forced targets, adds paired code and mathematics evaluations, and characterizes the offset constraints required for D4-equivariant row-major relative-score attention. Combining Reasoning-State Masking (RSM) with presentation randomization (PR) yields promising recipe-level results on Sudoku and mazes. The formalization and matched controls are thoughtful, but the distinction between sampling variation and presentation dependence, the incremental benefit of reasoning-state structure, and large-model reproducibility require further work.

Critical strengths
  1. Forced-target construction and exact D4 transportation give the Sudoku evaluation a clear semantic foundation. Explicitly distinguishing equivariance from correctness is also important.
  2. The two-/three-class serialization-rigidity result is a concrete, nontrivial theoretical contribution, with an explicit treatment of the softmax ambiguity, self-edges, and scope assumptions.
  3. Density, puzzle-frequency, and target-weight controls, together with pseudo-orbit diagnostics, materially strengthen the study. The authors report near-equal endpoints and unresolved 100M gains rather than suppressing these qualifications.
Critical weaknesses

1.The large-model one-shot ANY/ALL gaps do not yet adequately isolate presentation dependence from decoding randomness. Tables 2 and 15 use one decode per view, while Appendix D does not fully specify determinism, temperature, noise/decoding order, or cross-view random coupling for these evaluations. Even a perfectly view-invariant stochastic solver with success probability p can produce ANY=1−(1−p)^8 and ALL=p^8 under independent sampling; at p=0.5 these are approximately 99.6% and 0.4%. The pseudo-orbit control for the small-model recipe study is valuable, but analogous controls are needed for the large-model, code, and mathematics diagnostics, or the authors should establish an appropriate deterministic comparison.

  1. A positive interaction does not establish superior endpoint reliability from RSM. In the matched study, RSM+PR and density-matched random-state+PR have sECR values of 45.67% versus 45.74% at 50M and 42.76% versus 42.73% at 100M, with differences unresolved by the reported intervals. The positive interaction partly reflects PR repairing the larger instability introduced by RSM without augmentation. This acknowledged finding should be central to the main presentation rather than secondary to the initial +8.3-point interaction. The additional solving gains are modest at 50M and unresolved at 100M. Equivalent density/weight-matched controls at 8B and on mazes are needed to establish the unique contribution of reasoning-state structure.

  2. Estimator bias and training uncertainty remain incompletely characterized. With K=16, both extrema and token-marginal KL estimates have finite-sample bias. The paper correctly notes that pseudo-orbit subtraction is not generally unbiased, but the main comparisons still rely on these estimates. Please provide K-convergence analyses, repeated-input nulls matched by success probability, and sampling-null calibration for token leakage. The matched study includes three fine-tuning seeds, but its intervals condition on those runs; maze initialization checkpoints are not independent training repetitions. Training variation and test-puzzle uncertainty should be reported separately.

Questions for authors

see in weakness

5 comments
AuthorsOpenReview ↗

Response to Reviewer vGte (1/4)

We thank the reviewer for the careful review and the precise statistical suggestions, which we have followed below.

(Table numbers in this response refer to the original submission. In the revised PDF: original Table 2 → Table 1; Table 4 and Table 8 → Table 11; Table 15 → Table 23; Tables 17–18 → Tables 26–27. New results: decoding controls in Table 7 and Table 24, three-seed recipes in Tables 3 and 14–15, matched factorial in Table 28, token calibration in Table 29, refresh intervention in Table 30, matched mazes in Table 22, AR baselines in Tables 8–9, inference baselines in Table 10.)


W1. The gaps are not decoding randomness.

Table 2 uses greedy decoding, which has no sampling noise, so every recorded flip is caused by the change of presentation. The bound ANY = 1 − (1 − p)^8 assumes independent sampling per view and therefore does not apply: a view-invariant model decoded greedily has ANY = ALL.

To test whether the gap also persists when sampling noise is added, we extend the pseudo-orbit control (Appendix A.6) to the large-model, code, and MATH evaluations. For each problem with m equivalent presentations (m = 8 for Sudoku, m = 2 for code and MATH), we compare:

  • Pseudo-orbit: the original presentation sampled m times.
  • Real orbit: each of the m presentations sampled once.

Both contain the same sampling noise. For the reviewer's view-invariant stochastic solver, ANY and ALL, and hence the ANY − ALL gap, would be the same for the pseudo-orbit and the real orbit. Values below are ALL / ANY (gap = ANY − ALL), in %.

TaskModelPseudo-orbitReal orbitGap increase
Sudoku AC16LLaDA-8B36.2 / 52.0 (15.8)1.3 / 98.6 (97.3)+81.5
Sudoku AC24LLaDA-8B11.4 / 22.4 (11.0)0.0 / 73.5 (73.5)+62.5
Sudoku AC32LLaDA-8B1.4 / 6.2 (4.8)0.0 / 26.6 (26.6)+21.8
Sudoku AC24Dream-7B75.0 / 89.8 (14.8)50.5 / 100.0 (49.5)+34.7
Sudoku AC32Dream-7B55.1 / 74.4 (19.3)17.4 / 99.9 (82.6)+63.2
Sudoku AC32iLLaDA-8B71.8 / 75.4 (3.6)23.0 / 99.0 (76.0)+72.4
Sudoku AC32LLaDA-MoE48.6 / 68.6 (20.0)6.3 / 99.8 (93.5)+73.5
CodeLLaDA-8B37.3 / 53.6 (16.3)28.5 / 57.6 (29.1)+12.8
CodeDream-7B40.9 / 59.3 (18.4)29.3 / 62.7 (33.4)+15.0
CodeiLLaDA-8B21.7 / 36.0 (14.3)15.3 / 43.2 (27.9)+13.6
CodeLLaDA-MoE33.6 / 59.0 (25.4)25.8 / 60.7 (34.9)+9.5
MATH-500LLaDA-8B16.8 / 29.4 (12.5)16.2 / 33.7 (17.5)+5.0
MATH-500Dream-7B14.3 / 17.5 (3.3)9.1 / 19.2 (10.1)+6.8
MATH-500iLLaDA-8B†17.3 / 30.5 (13.2)14.2 / 30.5 (16.3)+3.1
MATH-500LLaDA-MoE18.7 / 39.5 (20.8)17.5 / 42.1 (24.6)+3.8

Sudoku and code use T = 0.5; MATH uses T = 0.2, since Dream-7B's outputs collapse to empty strings at T = 0.5. †200 of 582 pairs; the full set will be added to the final version.

In every one of the 15 settings, the ANY − ALL gap is larger across presentations than when the same presentation is resampled: by 22–82pp on Sudoku and 10–15pp on code, in every model, and by 3–7pp on MATH. Since both settings contain the same sampling noise, this additional gap is attributable to presentation. All reported Sudoku and code gap-increase 95% intervals exclude zero. On MATH, LLaDA-8B gives +5.0 [0.9, 9.0] pp and Dream-7B +6.8 [4.0, 9.8] pp; the iLLaDA and MoE MATH differences are positive but unresolved. We therefore do not treat those latter two settings as individually resolved.

The same control on the Table 15 checkpoints (LLaDA-8B LoRA, Sudoku-AC48, n = 500, m = 8):

RecipePseudo-orbitReal orbitGap increase
Canonical SFT87.6 / 87.6 (0.0)48.2 / 99.8 (51.6)+51.6
PR89.4 / 89.4 (0.0)49.8 / 100.0 (50.2)+50.2
RSM94.4 / 94.6 (0.2)74.6 / 99.8 (25.2)+25.0
RSM+PR98.2 / 98.2 (0.0)87.2 / 100.0 (12.8)+12.8

Under sampling, every fine-tuned model gives essentially the same correctness when a presentation is resampled (pseudo-orbit gap of at most 0.2pp), so the real-orbit gap is presentation-induced. It falls from 51.6pp (canonical SFT) and 50.2pp (PR) to 25.0pp (RSM) and 12.8pp (RSM+PR): PR reduces it by 1.4pp on its own but by 12.2pp on top of RSM.

AuthorsOpenReview ↗

Response to Reviewer vGte (2/4)

W2. Endpoint superiority and the factorial effect are different questions

The matched sECR endpoint does not establish a normalized-reliability advantage for RSM+PR over density-matched random+PR. The 50M contrast is −0.07 [−1.01, 0.83]. We therefore separate endpoint superiority from the factorial question.

Under full matching of puzzle frequency, hidden-cell count, and every target's expected supervision weight, the RSM × PR interaction is

Interaction50M100M
Mean success+1.51 [1.04, 1.98]+2.45 [1.89, 3.01]
sECR+4.06 [2.61, 5.56]+6.32 [4.70, 7.92]
Positive training seeds5/53/3

The interaction is therefore present in mean success itself, not only in an extrema-based ratio. At 100M, the same PR intervention lowers mean success on weight-matched random states by 1.00 [0.64, 1.37] pp but raises it on reasoning states by 1.44 [0.84, 2.04] pp.

Thus the unresolved normalized-reliability endpoint does not erase the factorial result. PR has a different, here opposite, effect under the two supervised-state distributions.

The endpoints also differ in absolute success. At 50M, RSM+PR exceeds density-matched random+PR by +0.94 [0.57, 1.29] pp in mean success and +0.66 [0.10, 1.22] pp in estimated worst-view success. The weight-matched contrasts are +0.85 [0.52, 1.20] and +0.60 [0.04, 1.15]. On the 272 puzzles the solver oracle cannot finish, the gain is +1.22 [0.74, 1.72].

Mechanism. A separately manipulated training variable tracks the interaction

The factorial establishes effect modification. We then tested a proposed learning-signal mechanism with a distinct intervention.

At a common pretrained checkpoint, under independent state draws and blockwise reuse of a presentation, the covariance of the averaged gradient is

Σn+αC\frac{\Sigma}{n}+\alpha C

where CC is the covariance of puzzle-averaged gradients across presentations and

α=∑bnb(nb−1)n2\alpha=\frac{\sum_b n_b(n_b-1)}{n^2}

is determined by the presentation-refresh schedule. Fresh PR removes this reuse component, not ordinary finite-sample gradient noise.

In the declared last-two-blocks-plus-head projection, tr⁡(C)\operatorname{tr}(C) is approximately 11× larger for reasoning states than for matched random states before fine-tuning. The measured difference is

1.78×10−4 [1.51×10−4, 2.07×10−4]1.78\times10^{-4}\ [1.51\times10^{-4},\,2.07\times10^{-4}]

We then trained separate three-seed models while changing presentation refresh. The sECR interaction moves

0.06 → 2.44 → 3.13 → 4.30 pp

from fixed to fresh presentations. A nested-random trajectory control, which uses no reasoning solver, gives a smaller positive interaction, +1.74 [0.66, 2.90].

The fixed-checkpoint identity is not being used as a theorem about final performance. The empirical point is that a presentation-dependent learning signal measured before training is substantially larger on reasoning states, and independently trained models move in the predicted direction when the corresponding refresh variable is manipulated.

The requested matched maze control is complete

At 100M, we compare RSM+PR with random-state+PR while matching state density, target weights, and the online PR procedure. Across three independent fine-tuning seeds and 500 held-out mazes, mean success rises from 92.0% to 94.1%, a gain of +2.10 [1.58, 2.67] pp. Thus the positive solving contribution of reasoning-state structure is not confined to Sudoku.

The corresponding maze sECR contrast is +0.74 [−0.17, 1.63], so we claim a matched solving gain, not a resolved normalized-reliability gain.

The submitted 8B experiment provides recipe-level, not matched, evidence, so we do not infer matched attribution from Table 15. It does show the same pattern: PR narrows the cross-view gap by only 1.4pp over canonical SFT but by 12.2pp over RSM. A density-matched 8B comparison is in progress and will be added to the final manuscript.

AuthorsOpenReview ↗

Response to Reviewer vGte (3/4)

W3. The central result survives measurements that do not use sampled extrema.

We agree with the statistical point behind W3: R^min\hat{R}{min}, C^max\hat{C}{max}, and sECR inherit finite-KK extrema bias. We therefore no longer make the extrema-based statistic carry the population-level conclusion. Instead we evaluate the claim three independent ways.

1. An exactly unbiased population-dispersion estimand

Let V(x)=1m∑g[pg(x)−pˉ(x)]2,H=I−1m11⊤V(x) = \frac{1}{m} \sum_g [p_g(x)-\bar p(x)]^2, \qquad H = I - \frac{1}{m}\mathbf{1}\mathbf{1}^\top For independent replicate vectors S(k)S^{(k)}, V^(x)=1mK(K−1)∑k≠ℓS(k)⊤HS(ℓ)\widehat{V}(x) = \frac{1}{mK(K-1)} \sum_{k\ne\ell} S^{(k)\top}HS^{(\ell)} satisfies E[V^(x)]=V(x)\mathbb{E}[\widehat{V}(x)] = V(x) for every K≥2K \ge 2. No extrema or ratio appear, and arbitrary dependence among views within one replicate is allowed. Negative finite-sample estimates are retained rather than clipped.

The favorable dispersion-reduction interaction J=(VC−VD)−(VA−VB)J = (V_C-V_D) - (V_A-V_B) is:

  • +0.00289 [0.00185, 0.00394] at 50M
  • +0.00440 [0.00338, 0.00548] at 100M

Thus the interaction survives on a population target whose expectation has no finite-KK extrema bias at any K≥2K \ge 2.

This also changes the role of the requested KK-convergence analysis. The central VV-based conclusion does not require extrapolating K→∞K \rightarrow \infty. Its estimator is unbiased at every admissible KK. We will additionally report the requested K′≤16K' \le 16 subsampling curves for the original extrema-based summaries in the final version, but we do not use an uncomputed convergence curve as evidence here.

2. The extrema-based result is attenuated by finite-KK calibration, but not eliminated.

Under mutually independent Bernoulli decodes with equal per-view success, conditioning on a problem's total number of successes gives: ∏g(Kng)(mKt)\frac{\prod_g \binom{K}{n_g}}{\binom{mK}{t}} The arm-wise conditional tests reject view-invariant success at the Monte Carlo floor (p=0.001p=0.001). This is an arm-wise null test, not a test of the sign of the factorial interaction.

Separately, a pooled-success plug-in reference leaves sECR interactions of +2.96 pp at 50M and +4.45 pp at 100M after calibration.

We therefore report the original extrema metrics for continuity but do not use them as the primary population evidence. The plug-in calculation is a reference calibration, not an exact unbiased decomposition, so we do not label a literal fraction of the original interaction as "artifact."

Comments on the paper

1 comment
AuthorsOpenReview ↗

Revised paper uploaded: summary of changes

We thank all reviewers again. We have uploaded a revised PDF and supplementary code. Detailed answers are in each thread. The main additions are:

  • Decoding noise (vGte, hMSt, ZRTZ). A sampling control on every setting of the large-model table (Table 1 in the revision, Table 2 in the submission) shows that switching presentations widens the ANY − ALL gap well beyond resampling the same input: by 22–82 pp on Sudoku and 10–15 pp on code (App. B.3).
  • Matched controls (vGte, hMSt, ByqZ). With puzzles, density, and target weights matched, the RSM × PR interaction holds at 50M and 100M across all seeds (Sec. 5.3). At 8B, RSM+PR exceeds matched random+PR by 33.5 pp in all-view correctness, and on mazes by 2.10 pp in mean success (Sec. 5.5).
  • Seeds and estimators (vGte, hMSt). The 50M recipe study (Table 4 in the submission) is repeated with three seeds, with RSM+PR first in every seed (Table 3), and an unbiased dispersion estimator complements the extrema-based summaries (Sec. 3.3).
  • Mechanism, baselines, and code (all reviewers). A refresh intervention for why PR helps reasoning states more (Sec. 4.5 and 5.4), inference-time and AR baselines (Sec. 5.6, App. B.4–B.5), and the complete code with a README.

Why this matters. Accuracy on a single presentation hides whether a model has solved a problem or only one form of it. The canonical 8B model is 88.2% accurate, yet solves every presentation of a puzzle only 47.7% of the time. This is not a property of one model family: Qwen2.5-7B solves 57.5% of views but all eight views of a puzzle 1.6% of the time. The paper gives a test any model can take, a theorem showing that standard positional attention does not supply the symmetry, and evidence that it can be trained: RSM+PR raises the 8B model's all-view correctness to 86.1%. As language models take on code, mathematics, and planning, where one problem has many equivalent forms, a model that is right in only some of them cannot be relied on.

We thank the reviewers and the area chair for their time, and we welcome any remaining questions before the discussion closes.

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

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