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Desk rejected at ICLR 2027

Quantizing Diffusion LLMs Under Parallel Decoding: Commitment Risk and the Parallelism Tax

Desk rejected at ICLR 2027, so left out of the paper lists and the map.

Abstract

Diffusion large language models (dLLMs) are served with accelerated decoders that cache context and commit, in one step, every masked position whose confidence clears a threshold. Yet post-training quantization of dLLMs has so far been calibrated and evaluated under fixed-step samplers without caching. We study W4A4 quantization under the deployed decoder and find that the decoder determines both where quantization harms accuracy and what it costs. Irreversible errors enter chiefly through forced commitments, made when no position clears the threshold: they are a minority of commitments but carry most quantization-induced flips. Quantization also levies a parallelism tax, extra forward passes per response: by compressing top logit gaps, it pushes positions below the threshold while leaving predictions largely intact. We propose DECAL, which reweights layer-wise calibration by a commitment-risk prior measured on the deployed decoder, and an argmax-preserving commit temperature that recovers the tax. On LLaDA and Dream, DECAL attains the best average accuracy among W4A4 methods, with lower run-to-run variance than prior calibration.

Primary area:
generative models
Keywords:
diffusion language models, post-training quantization

Reviews

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1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_Y31zOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies post-training quantization of diffusion LLMs under Fast-dLLM's cached parallel decoding, and shows that quantization interacts with the confidence-based decoding policy. The authors identify two effects: quantization errors are concentrated in forced commitments, and quantization can reduce confidence and harming decoding parallelism. Based on these observations, they propose DECAL, which reweighs calibration positions considering commitment risk and downstream impact. Experiments on LLaDA-8B-Instruct and Dream-7B show higher W4A4 accuracy recovery over prior calibration methods and reduced parallelism overhead.

Critical strengths
  1. The core insight of this paper is clear. The paper identifies two practical dLLM-specific issues caused by quantization under parallel decoding, i.e., errors concentrated in forced commitments and reduced decoding parallelism. The proposed method is designed accordingly, and the experiments show accuracy improvements over the calibration baselines.

  2. The experimental analysis and temperature study are sound. The same-state full-precision shadow comparisons in Section 3 help isolate quantization-induced changes in token predictions and commitment decisions from different decoding trajectories, while the temperature study in Section 5.4 provides empirical support for the confidence-deflation explanation of the parallelism tax.

Critical weaknesses
  1. For masked diffusion LLMs, the current high-performing models are native block-diffusion model, e.g., LLaDA2.0 [1]. However, while the method seems to be effective, the paper's experiments use two full-sequence diffusion models in 2025, and with block-wise decoding schedule of Fast-dLLM only. I didn't find the method conflicts with block-diffusion models but experiments covering this aspect should be presented.

  2. In Section 5.3’s ablation, the flip-only and reach-only variants also perform well and are close to/sometimes better than full DECAL, leaving the benefit of combining the two factors less convincing.

Reference:

[1] Tiwei Bie et al., LLaDA2.0: Scaling Up Diffusion Language Models to 100B, arXiv 2025.

Questions for authors
  1. Token and placement flips are both induced by the same quantized confidences, while Eq. (2) models their margin with a zero-mean Gaussian assumption and combines them under an independence assumption. How accurate are these assumptions in practice?

  2. How was the concentration parameter $(c)$ selected for each model? Is the performance sensitive to this choice?

8 comments
AuthorsOpenReview ↗

Response to Reviewer Y31z (1/4)

We thank the reviewer for the positive assessment and the constructive suggestions, and for finding the core insight clear and our analyses sound. In brief: on the block-diffusion model Fast-dLLM v2 [1], forced commitments are as common as on LLaDA, quantization levies a parallelism tax, and DECAL improves W4A4 accuracy; the single factors look alike because they nearly coincide on LLaDA, and a new control shows that the gain comes from decoder-aligned placement; the assumptions of Eq. (2) are close to the data and do not change the prior; and the concentration parameter cc only sets how concentrated the prior is, not the placement that carries the gain.

W1. Experiments on block-diffusion models

We added Fast-dLLM v2 [1] (v2 below), a native block-diffusion model adapted from Qwen2.5-Instruct [2], at 1.5B and 7B parameters. Among current block-diffusion models, it gives the cleanest test: its layers are dense like those of LLaDA and Dream, its 7B model is adapted, like Dream-7B, from Qwen2.5-7B (here its instruction-tuned version), and its decoder is the block-diffusion successor of Fast-dLLM, so block decoding is the main change from the paper’s setting. LLaDA2.0 [3], which the reviewer mentions, uses mixture-of-experts layers at 16B and 100B parameters and would change architecture and scale together with the decoding scheme.

Fast-dLLM v2 decodes blocks of 32 tokens from left to right with exact caching of completed blocks, and commits inside each block, in sub-blocks of 8 tokens, with the same threshold rule as Fast-dLLM (τ = 0.9). DECAL is applied unchanged, with its prior collected under v2’s own decoder.

Forced commitments and the parallelism tax carry over

Forced commitments are as common as in the paper: under W4A4, 10% to 15% of the commitments in the returned output are forced, close to the 16.5% on LLaDA (Section 3.2). Quantization lowers the number of tokens written per forward pass and raises the share of forced commitments (Table R1); the resulting tax, 7.6% on v2-1.5B and 14.0% on v2-7B, is well above FlatQuant’s 0.8% and 2.8% on LLaDA and Dream (Figure 1c).

Table R1. Parallelism tax on Fast-dLLM v2 (200 GSM8K prompts, τ = 0.9, W4A4 FlatQuant). Forward passes are counted per returned token, so answer length does not enter.

ModelTokens per forward pass (FP16 → W4A4)Extra forward passesForced commitments (FP16 → W4A4)
v2-1.5B2.10 → 1.95+7.6%12.6% → 15.4%
v2-7B2.58 → 2.27+14.0%8.2% → 10.2%

Accuracy on v2-7B

Table R2. W4A4 accuracy (%) on Fast-dLLM v2-7B (τ = 0.9; mean ± std over three calibration runs).

MethodGSM8KMATHAvg.
FP1682.1146.0764.09
FlatQuant77.94 ± 0.7739.05 ± 0.6458.49
DECAL79.02 ± 1.6939.97 ± 0.5259.50

DECAL improves on FlatQuant by 1.1 points on GSM8K and 0.9 on MATH (Table R2), closing about a fifth of the gap to full precision, in line with its gains in Table 1.

AuthorsOpenReview ↗

Response to Reviewer Y31z (2/4)

W2. The single-factor variants perform close to the full prior

We agree that Table 3 does not separate the product from the stronger single factor, and we have softened this claim in Section 5.3. A new control shows what the ablation does establish: the gain comes from where the calibration budget is placed, not from non-uniform weighting as such. We shuffled DECAL’s prior over the 256 window positions and calibrated with the protocol of Table 3: the weights keep their mean, spread and range but lose their alignment with the decoder.

Table R3. Table 3 with the shuffled control added (W4A4, dual cache, mean of two calibration runs).

PriorLLaDA GSM8KLLaDA MATHLLaDA Avg.Dream GSM8KDream MATHDream Avg.
Uniform74.9128.2251.5766.0023.1144.56
Shuffled DECAL prior (new)74.6828.4751.5866.4624.7945.63
Flip probability only76.0429.3252.6867.7824.8146.30
Reach only76.1729.1152.6465.9725.8945.93
DECAL (product)76.6528.8552.7567.7424.9046.32

On LLaDA, the shuffled prior is no better than uniform (51.58 against 51.57; Table R3), while every decoder-aligned prior gains 1.1 to 1.2 points. FAIR-Calib’s prior, also non-uniform but unrelated to ours (rank correlation −0.20), likewise adds only 0.3 points on these tasks (Table 1). On Dream, the shuffled prior is the weakest non-uniform variant. Placement, not non-uniformity, carries the gain.

The single factors look alike on LLaDA because they nearly coincide there (rank correlation 0.85 between them, and at least 0.95 with the product): fragile commitments sit early in the response, where reach is also highest. On Dream, a base model that writes past its answer, they diverge (rank correlation −0.33), and the better single factor depends on the task (flip probability on GSM8K, reach on MATH). We keep the product because it is the expected damage of an error (a flip that reaches the output), so it needs no per-model or per-task choice of factor, and it has the best average on both models.

Why this particular weighting. Each factor of the product is also supported on its own. The risk factor puts the right commitments first: ranked by the full-precision margin from which π is computed, a commitment whose token flips is rated riskier than one whose token does not in 98.7% of pairs on LLaDA and 93.9% on Dream (see our answer to Q1). The decisions it marks are also the ones that matter: when only the forced commitments of W4A4 (on Dream, also the unconditional write at the start of each block) take the full-precision choice, 30 of 33 (LLaDA) and 32 of 36 (Dream) GSM8K answers broken by quantization become correct again. The reach factor rests on a premise we verified, that the errors picked up over later reads are approximately independent (Appendix F), and it carries signal by itself: the reach-only prior beats uniform weighting by 1.1 (LLaDA) and 1.4 (Dream) average points (Table 3). The product thus weights each position by a quantity that is both measurable and decisive for the answer.

AuthorsOpenReview ↗

Response to Reviewer Y31z (3/4)

Q1. How accurate are the Gaussian and independence assumptions of Eq. (2)?

In short, both assumptions are close to the data, and neither changes the prior. Since Eq. (4) normalizes the prior, DECAL uses only the order of positions. We checked each part of Eq. (2) against the flips recorded for Figure 1b (W4A4 FlatQuant, first 400 GSM8K test questions; 102,400 commitments on LLaDA and 99,200 on Dream).

Smaller margins do flip more often. The margin is the lead of the top token over the runner-up at full precision, and π grows as it shrinks. Take any commitment whose token flips and any whose token does not: the one that flips has the smaller margin in 98.7% of such pairs on LLaDA and 93.9% on Dream, where a random ordering would give 50% (this is the AUROC, 0.987 and 0.939).

Quantization does not push in a fixed direction (zero mean). If quantization systematically favored the written token, near ties would rarely flip; if it favored the runner-up, they would flip most of the time. Without a preferred direction, a near tie is a coin toss, and this is what we observe: among commitments with a margin below 0.1, 47% flip on LLaDA and 51% on Dream.

The Gaussian curve matches the observed flip rates. Eq. (2) assumes that the flip rate falls with the margin along a Gaussian curve. With its single scale fitted to the data, this curve differs from the observed rates by only 0.1 percentage points on average on LLaDA and 0.8 on Dream. The default scale s=m~s = \tilde{m}, which must be fixed before the quantizer is known, makes the predicted probabilities too high in absolute terms; DECAL is unaffected, because it uses only their order (see the last point).

Treating the two kinds of failure as independent is a close approximation. A forced commitment can fail by writing the wrong token or by choosing the wrong position. As the reviewer notes, both stem from the same confidences; they are slightly correlated (about 0.1) but rarely occur together, so treating them as independent barely changes how often a forced commitment fails: 37.8% predicted against 39.4% observed on LLaDA, and 39.8% against 39.2% on Dream.

The prior does not depend on these modeling choices. We rebuilt the prior with the Gaussian curves replaced by flip rates measured directly from the data, so that no assumed distribution enters. The rebuilt prior orders the 256 window positions almost exactly as ours: the rank correlation between the two is 0.994 on LLaDA and 0.997 on Dream, where 1 means an identical order.

Reviewer_An7yOpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
3
Soundness
3
Read review
Paper summary

The paper’s central finding is that quantization affects both accuracy and decoding parallelism. The authors identify two problems:

  1. Forced commitments concentrate quantization-induced errors.
  2. Quantization creates a “parallelism tax.”
Critical strengths
  • The paper recognizes that quantization changes the decisions controlling inference cost, as well as numerical accuracy. This is a useful advance over evaluations restricted to fixed-step sampling or teacher-forced metrics.
  • Quantization can alter both the predicted token and the position selected for forced commitment. The concentration of permanent flips in forced commitments provides a concrete motivation for commitment-aware calibration.
Critical weaknesses
  • Under cached decoding, DECAL improves average accuracy over FAIR-Calib by only 0.36 points on LLaDA and 0.69 points on Dream. Several task-level differences are small relative to calibration-run variability.
  • The proposed product of flip probability and reach is intuitively appealing, but Table 3 shows average gains of only 0.07 and 0.02 points over the stronger single-factor variant on LLaDA and Dream, respectively. These results establish the value of nonuniform weighting more clearly than the necessity of the particular product formulation.
  • The risk and propagation models are heuristic
  • The guarantees do not establish end-to-end safety or monotonicity
Questions for authors
  • Can you provide paired confidence intervals across evaluation examples and additional calibration seeds for DECAL’s improvement over FAIR-Calib?
  • How well do predicted flip probabilities match observed flip frequencies?
  • Given the small advantage over single-factor priors, what evidence establishes that multiplying risk by reach is necessary?
  • How do the findings and benefits of DECAL extend to adaptive decoding methods such as Polestar [1], which uses representation drift to guide cache refreshes and token commitment? Evaluating W4A4 Polestar with standard versus DECAL calibration would help establish whether forced commitments remain the dominant source of quantization-induced errors and whether the parallelism tax persists. An accuracy–throughput comparison under matched precision and evaluation settings would also clarify the additional benefit of commitment-temperature calibration over drift-guided commitment.

[1] Lee, Mingyu, et al. "Polestar: Drift-Aware Cache Calibration and Token Commitment for Efficient Inference of Diffusion LLMs." arXiv preprint arXiv:2607.14107 (2026).

6 comments
AuthorsOpenReview ↗

Response to Reviewer An7y (1/4)

We thank the reviewer for the thorough review and for recognizing that quantization changes the decisions that control inference cost, and that the concentration of flips in forced commitments motivates commitment-aware calibration. In brief: DECAL beats FAIR-Calib on the four-task average for all six new calibration seeds; its gain requires decoder-aligned placement, since the same weights at random positions do not help; the flip-probability model ranks risk accurately and its assumptions do not change the prior; and under the drift-guided commitment of Polestar [1], forced commitments still carry most errors, the parallelism tax persists, and both DECAL and the commit temperature keep their benefits.

W1 and Q1. Paired confidence intervals and additional calibration seeds

We repeated the calibration of both methods with six new random seeds. Within a seed, both methods use the same 128 WikiText-2 sequences and initialization, so the results are paired; everything else is as in Table 1 (LLaDA-8B-Instruct, dual cache, τ = 0.9).

Table R1. W4A4 accuracy (%) for six calibration seeds. Each cell: DECAL / FAIR-Calib; bold: the better of the pair. Δ: DECAL − FAIR-Calib on the four-task average. Absolute values differ slightly from Table 1 because each seed draws its own calibration set.

SeedGSM8KHumanEvalMBPPMATHAvg.Δ
176.42 / 75.0634.15 / 35.9835.80 / 34.8029.29 / 27.7943.91 / 43.40+0.51
275.59 / 75.0635.37 / 32.9334.60 / 34.0028.57 / 28.4343.53 / 42.60+0.93
376.04 / 75.5936.59 / 34.1534.60 / 33.6029.07 / 26.5744.07 / 42.48+1.59
474.68 / 74.4535.37 / 34.7636.00 / 35.0028.64 / 29.4343.67 / 43.41+0.26
575.36 / 74.9836.59 / 34.1534.80 / 36.0029.21 / 28.7943.99 / 43.48+0.51
675.28 / 74.3035.98 / 34.1538.00 / 37.4028.36 / 28.4344.40 / 43.57+0.83
Mean75.56 / 74.9135.67 / 34.3535.63 / 35.1328.86 / 28.2443.93 / 43.16+0.77
Std0.61 / 0.470.92 / 1.001.31 / 1.390.38 / 0.980.31 / 0.48

DECAL is ahead on the four-task average for every seed (Table R1), by 0.26 to 1.59 points (+0.77 on average, against +0.36 in Table 1), and on 20 of the 24 seed–task pairs. Its four-task average also varies less across seeds (standard deviation 0.31 against 0.48).

Table R2. Paired tests of the average gain.

Paired comparison (DECAL − FAIR-Calib, Avg.)Gain95% CITest
Across calibration seeds (6 seeds)+0.77[+0.28, +1.27]t-test p = 0.010
Across questions (3,383 questions, 6 seeds pooled)+0.77[+0.06, +1.51]paired bootstrap

Both intervals in Table R2 exclude zero. A rank-based test that does not assume normality agrees (Wilcoxon, p = 0.031, the smallest value possible with six seeds), and GSM8K alone is also significant (p = 0.013). Question by question, DECAL is more often the only method to answer correctly, on every task (Table R3).

Table R3. Questions answered correctly by one method but not the other, summed over the six seeds.

GSM8KHumanEvalMBPPMATH
Only DECAL correct70475214618
Only FAIR-Calib correct65262199566
AuthorsOpenReview ↗

Response to Reviewer An7y (2/4)

W2 and Q3. Is multiplying risk by reach necessary?

We agree that Table 3 does not separate the product from the stronger single factor, and we have softened this claim in Section 5.3. A new control shows what the ablation does establish: the gain comes from where the calibration budget is placed, not from non-uniform weighting as such. We shuffled DECAL’s prior over the 256 window positions and calibrated with the protocol of Table 3: the weights keep their mean, spread and range but lose their alignment with the decoder.

Table R4. Table 3 with the shuffled control added (W4A4, dual cache, mean of two calibration runs).

PriorLLaDA GSM8KLLaDA MATHLLaDA Avg.Dream GSM8KDream MATHDream Avg.
Uniform74.9128.2251.5766.0023.1144.56
Shuffled DECAL prior (new)74.6828.4751.5866.4624.7945.63
Flip probability only76.0429.3252.6867.7824.8146.30
Reach only76.1729.1152.6465.9725.8945.93
DECAL (product)76.6528.8552.7567.7424.9046.32

On LLaDA, the shuffled prior is no better than uniform (51.58 against 51.57; Table R4), while every decoder-aligned prior gains 1.1 to 1.2 points. FAIR-Calib’s prior, also non-uniform but unrelated to ours (rank correlation −0.20), likewise adds only 0.3 points on these tasks (Table 1). On Dream, the shuffled prior is the weakest non-uniform variant. Placement, not non-uniformity, carries the gain.

The single factors look alike on LLaDA because they nearly coincide there (rank correlation 0.85 between them, and at least 0.95 with the product): fragile commitments sit early in the response, where reach is also highest. On Dream, a base model that writes past its answer, they diverge (rank correlation −0.33), and the better single factor depends on the task (flip probability on GSM8K, reach on MATH). We keep the product because it is the expected damage of an error (a flip that reaches the output), so it needs no per-model or per-task choice of factor, and it has the best average on both models.

Each factor is also validated on its own; we summarize this evidence in our answer to W3.

Q2. How well do predicted flip probabilities match observed flip frequencies?

In short, π ranks commitments by risk almost perfectly, and with its scale fitted to the data it also matches the observed flip rates. DECAL uses only the ranking, since Eq. (4) normalizes the prior. We checked each part of Eq. (2) against the flips recorded for Figure 1b (W4A4 FlatQuant, first 400 GSM8K test questions; 102,400 commitments on LLaDA and 99,200 on Dream).

Smaller margins do flip more often. The margin is the lead of the top token over the runner-up at full precision, and π grows as it shrinks. Take any commitment whose token flips and any whose token does not: the one that flips has the smaller margin in 98.7% of such pairs on LLaDA and 93.9% on Dream, where a random ordering would give 50% (this is the AUROC, 0.987 and 0.939).

Quantization does not push in a fixed direction (zero mean). If quantization systematically favored the written token, near ties would rarely flip; if it favored the runner-up, they would flip most of the time. Without a preferred direction, a near tie is a coin toss, and this is what we observe: among commitments with a margin below 0.1, 47% flip on LLaDA and 51% on Dream.

The Gaussian curve matches the observed flip rates. Eq. (2) assumes that the flip rate falls with the margin along a Gaussian curve. With its single scale fitted to the data, this curve differs from the observed rates by only 0.1 percentage points on average on LLaDA and 0.8 on Dream. The default scale s=m~s = \tilde{m}, which must be fixed before the quantizer is known, makes the predicted probabilities too high in absolute terms; DECAL is unaffected, because it uses only their order (see the last point).

Treating the two kinds of failure as independent is a close approximation. A forced commitment can fail by writing the wrong token or by choosing the wrong position. Both depend on the same confidences and are slightly correlated (about 0.1), but they rarely occur together, so treating them as independent barely changes how often a forced commitment fails: 37.8% predicted against 39.4% observed on LLaDA, and 39.8% against 39.2% on Dream.

The prior does not depend on these modeling choices. We rebuilt the prior with the Gaussian curves replaced by flip rates measured directly from the data, so that no assumed distribution enters. The rebuilt prior orders the 256 window positions almost exactly as ours: the rank correlation between the two is 0.994 on LLaDA and 0.997 on Dream, where 1 means an identical order.

AuthorsOpenReview ↗

Response to Reviewer An7y (3/4)

W3. The risk and propagation models are heuristic

Both models serve only to rank positions, because Eq. (4) keeps nothing but their order. What matters is therefore whether they rank correctly, and the data confirm each part.

The risk model singles out the commitments that flip. As shown in our answer to Q2, the full-precision margin from which π is computed rates a flipped commitment riskier than an unflipped one in 98.7% (LLaDA) and 93.9% (Dream) of pairs, and dropping the Gaussian assumption leaves the order of positions almost unchanged.

The commitments it flags are the ones that decide answers. When W4A4 takes the full-precision choice only at its forced commitments (on Dream, also at the unconditional write at the start of each block), 30 of the 33 (LLaDA) and 32 of the 36 (Dream) GSM8K answers broken by quantization become correct again (400 questions of Figure 1b).

The square root in the reach model matches how errors add up. Every later pass that reads a flipped token adds a small perturbation. These perturbations are nearly independent: the terms through which they would reinforce one another are only 3.6% of the size of the individual terms (Appendix F). Independent perturbations add up like random noise, growing with the square root of their number, which is the form of Eq. (3); a logarithm in its place changes the prior very little (correlation 0.9975).

Reach carries signal on its own. The reach-only prior beats uniform weighting by 1.1 (LLaDA) and 1.4 (Dream) average points (Table 3). As the shuffled control shows, such gains require the weight to sit at the right positions (Table R4).

W4. The guarantees do not establish end-to-end safety or monotonicity

We agree that the guarantees are per-state, and this is by design. Proposition 1 holds for every decoding state, but no change to when positions are committed, not even lowering τ, admits a trajectory-level guarantee, because an earlier commitment changes the context of every later step. We therefore prove the per-state properties and measure the trajectory-level ones. At the first early release in each question, the released token is the one the T = 1 schedule eventually writes in 98.7% to 99.4% of questions (Table C.1). Forward passes fall monotonically as T is lowered in every ladder we measured: under Fast-dLLM (Table C.1, Figure 4), and under drift-guided commitment, from 79.7 to 66.7 per response on the prompts used to calibrate TmatchT_{\text{match}} as T goes from 1 to 0.84 (Q4). This monotonicity is all that the calibration of Eq. (7) needs. At TmatchT_{\text{match}}, the accuracy change stays within run-to-run noise under Fast-dLLM (Section 5.4) and is not statistically significant under drift-guided commitment (Q4).

Reviewer_bXC5OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper studies W4A4 PTQ of diffusion LLMs under Fast-dLLM’s confidence-threshold decoder and makes two observations: (1) most quantization errors that reach the final answer come from forced writes, made when no token is confident enough, though these are only 16–29% of all writes; (2) quantization lowers confidence, so fewer tokens clear the threshold per step and responses need more forward passes. For (1), DECAL gives risky positions more weight during calibration. For (2), the paper lowers the effective confidence threshold until the quantized model uses as many forward passes as full precision. DECAL reaches the best average W4A4 accuracy on four benchmarks, and the threshold change removes the extra passes.

Critical strengths

The paper provides useful diagnosis of how quantization fails under the fast-dLLM decoding. It compares the quantized model against a full-precision copy run on the same decoding states, which pinpoints where and how quantization errors arise. The trouble shooting technique is different from perplexity and fixed-step evaluations used by prior work and brings new findings as summarized in the paper summary section.

Critical weaknesses
  1. The accuracy gain is small and not shown to be statistically significant. DECAL differs from FAIR-Calib only in how it weights calibration positions, and that change adds +0.36 average points on LLaDA and +0.69 on Dream. These gaps are below the run-to-run standard deviations (Table 1), also no significance test is reported. And DECAL is not best on MBPP. The ablation (Table 3) is similarly inconclusive: on both models, weighting by flip probability alone scores within 0.1, and reach alone is within 0.4 points of combining the two factors. So the evidence supports only that some non-uniform weighting helps, not that this particular one does. So it's unclear how effective the method is in addressing the challenge.

  2. Quantization lowers the model’s confidence, which both (1) slows decoding and (2) makes low-confidence writes easier to get wrong, the errors DECAL’s calibration targets. Beyond this shared cause, could the authors clarify how the slowdown and its fix relate to DECAL? Especially on FlatQuant-based models where slow down is small. Conversely, does fixing the slowdown reduce these forced-write errors? If not, the two contributions may be better presented as separate findings.

Questions for authors
  1. Is DECAL’s gain over FAIR-Calib statistically significant? The average gaps (+0.36 on LLaDA, +0.69 on Dream) are smaller than their standard error over three runs. A paired test across questions and more calibration runs would provide more information.

  2. Do forced-write errors actually cause wrong answers? How often do questions the quantized model gets wrong contain such an error, compared with questions it gets right? For example, when the top two tokens are nearly tied, either choice may be fine. Could the authors provide some insights into this.

  3. Does fixing the slowdown also reduce the forced-write errors DECAL targets? The commit temperature cuts forced steps by about 29% without a visible accuracy gain, so I wonder whether the two parts of the paper are more loosely connected than the framing suggests.

  4. Since the decoder knows when it makes a forced write, and the paper already intervenes at decoding time for speed, could a similar inference-time fix target accuracy, for example recomputing forced writes at higher precision? Even a negative result would be useful to show the need for a good calibration.

5 comments
AuthorsOpenReview ↗

Response to Reviewer bXC5 (1/4)

We thank the reviewer for the careful reading and precise questions, and for recognizing the value of comparing the quantized model with a full-precision copy on the same decoding states. In brief: DECAL beats FAIR-Calib on the four-task average for each of six new calibration seeds; correcting only the forced writes repairs about nine in ten answers that quantization breaks; and the commit temperature removes only forced writes that rarely err, which is why it speeds up decoding without changing accuracy. Following the review, we use the term “forced write” for what the paper calls a forced commitment.

W1 and Q1. Is DECAL’s gain over FAIR-Calib statistically significant?

We repeated the calibration of both methods with six new random seeds. Within a seed, both methods use the same 128 WikiText-2 sequences and initialization, so the results are paired; everything else is as in Table 1 (LLaDA-8B-Instruct, dual cache, τ = 0.9).

Table R1. W4A4 accuracy (%) for six calibration seeds. Each cell: DECAL / FAIR-Calib; bold: the better of the pair. Δ: DECAL − FAIR-Calib on the four-task average. Absolute values differ slightly from Table 1 because each seed draws its own calibration set.

SeedGSM8KHumanEvalMBPPMATHAvg.Δ
176.42 / 75.0634.15 / 35.9835.80 / 34.8029.29 / 27.7943.91 / 43.40+0.51
275.59 / 75.0635.37 / 32.9334.60 / 34.0028.57 / 28.4343.53 / 42.60+0.93
376.04 / 75.5936.59 / 34.1534.60 / 33.6029.07 / 26.5744.07 / 42.48+1.59
474.68 / 74.4535.37 / 34.7636.00 / 35.0028.64 / 29.4343.67 / 43.41+0.26
575.36 / 74.9836.59 / 34.1534.80 / 36.0029.21 / 28.7943.99 / 43.48+0.51
675.28 / 74.3035.98 / 34.1538.00 / 37.4028.36 / 28.4344.40 / 43.57+0.83
Mean75.56 / 74.9135.67 / 34.3535.63 / 35.1328.86 / 28.2443.93 / 43.16+0.77
Std0.61 / 0.470.92 / 1.001.31 / 1.390.38 / 0.980.31 / 0.48

DECAL is ahead on the four-task average for every seed (Table R1), by 0.26 to 1.59 points (+0.77 on average, against +0.36 in Table 1), and on 20 of the 24 seed–task pairs. Its four-task average also varies less across seeds (standard deviation 0.31 against 0.48).

Table R2. Paired tests of the average gain.

Paired comparison (DECAL − FAIR-Calib, Avg.)Gain95% CITest
Across calibration seeds (6 seeds)+0.77[+0.28, +1.27]t-test p = 0.010
Across questions (3,383 questions, 6 seeds pooled)+0.77[+0.06, +1.51]paired bootstrap

Both intervals in Table R2 exclude zero. A rank-based test that does not assume normality agrees (Wilcoxon, p = 0.031, the smallest value possible with six seeds), and GSM8K alone is also significant (p = 0.013). Question by question, DECAL is more often the only method to answer correctly, on every task (Table R3).

Table R3. Questions answered correctly by one method but not the other, summed over the six seeds.

GSM8KHumanEvalMBPPMATH
Only DECAL correct70475214618
Only FAIR-Calib correct65262199566

On MBPP, where the three FlatQuant-based methods are within one standard deviation of each other in Table 1, DECAL is ahead for five of the six seeds (35.63 against 35.13 on average, Table R1).

AuthorsOpenReview ↗

Response to Reviewer bXC5 (2/4)

W1 (continued). Does the ablation support this particular weighting?

We agree that Table 3 does not separate the product from the stronger single factor, and we have softened this claim in Section 5.3. A new control shows what the ablation does establish: the gain comes from where the calibration budget is placed, not from non-uniform weighting as such. We shuffled DECAL’s prior over the 256 window positions and calibrated with the protocol of Table 3: the weights keep their mean, spread and range but lose their alignment with the decoder.

Table R4. Table 3 with the shuffled control added (W4A4, dual cache, mean of two calibration runs).

PriorLLaDA GSM8KLLaDA MATHLLaDA Avg.Dream GSM8KDream MATHDream Avg.
Uniform74.9128.2251.5766.0023.1144.56
Shuffled DECAL prior (new)74.6828.4751.5866.4624.7945.63
Flip probability only76.0429.3252.6867.7824.8146.30
Reach only76.1729.1152.6465.9725.8945.93
DECAL (product)76.6528.8552.7567.7424.9046.32

On LLaDA, the shuffled prior is no better than uniform (51.58 against 51.57; Table R4), while every decoder-aligned prior gains 1.1 to 1.2 points. FAIR-Calib’s prior, also non-uniform but unrelated to ours (rank correlation −0.20), likewise adds only 0.3 points on these tasks (Table 1). On Dream, the shuffled prior is the weakest non-uniform variant. Placement, not non-uniformity, carries the gain.

The single factors look alike on LLaDA because they nearly coincide there (rank correlation 0.85 between them, and at least 0.95 with the product): fragile commitments sit early in the response, where reach is also highest. On Dream, a base model that writes past its answer, they diverge (rank correlation −0.33), and the better single factor depends on the task (flip probability on GSM8K, reach on MATH). We keep the product because it is the expected damage of an error (a flip that reaches the output), so it needs no per-model or per-task choice of factor, and it has the best average on both models.

Why this particular weighting. Each factor of the product is also supported on its own. The risk factor puts the right commitments first: ranked by the full-precision margin from which π is computed, a commitment whose token flips is rated riskier than one whose token does not in 98.7% of pairs on LLaDA and 93.9% on Dream. The decisions it marks are also the ones that matter: correcting only the forced writes repairs about nine in ten broken answers (Table R7 below). The reach factor rests on a premise we verified, that the errors picked up over later reads are approximately independent (Appendix F), and it carries signal by itself: the reach-only prior beats uniform weighting by 1.1 (LLaDA) and 1.4 (Dream) average points (Table 3). The product thus weights each position by a quantity that is both measurable and decisive for the answer.

Q2. Do forced-write errors actually cause wrong answers?

Yes, and causally: correcting only the forced writes repairs about nine in ten broken answers. The numbers in (a)–(d) come from the recordings behind Figure 1b (W4A4 FlatQuant, first 400 GSM8K test questions, Fast-dLLM with dual cache, τ = 0.9). A token flip is a write whose token differs from the one full precision would write in the same state; a question is broken if full precision answers it correctly and W4A4 does not, and kept if both do.

(a) Wrong answers contain more forced-write errors

Table R5. Average number of forced flips (token flips at forced writes) per question. CI: bootstrap over questions.

W4A4 wrongW4A4 rightBrokenKeptBroken − Kept
LLaDA-8B3.08 (n = 88)1.99 (n = 312)3.36 (n = 33)1.95 (n = 282)+1.4 (95% CI [0.6, 2.4])
Dream-7B3.90 (n = 121)2.81 (n = 279)4.36 (n = 36)2.70 (n = 252)+1.7 (95% CI [1.0, 2.4])

Many single forced flips are harmless, as the reviewer suggests (see (e)); what separates broken from kept questions is how many they contain (Table R5).

(b) The chance of a wrong answer rises with the number of forced flips

Table R6. Share of questions that full precision answers correctly but W4A4 gets wrong, by number of forced flips.

Forced flips0123–4≥ 5
LLaDA-8B4% (2 / 47)8% (7 / 84)5% (4 / 86)18% (13 / 73)28% (7 / 25)
Dream-7B0% (0 / 23)5% (3 / 56)7% (4 / 59)14% (13 / 95)29% (16 / 55)

The effect holds after controlling for question length and the number of forced writes: each additional forced flip multiplies the odds of a wrong answer by 1.25 on LLaDA and 1.24 on Dream (95% CI 1.01–1.57 and 1.01–1.55).

AuthorsOpenReview ↗

Response to Reviewer bXC5 (3/4)

Q2. Do forced-write errors actually cause wrong answers? (continued)

(c) The error that breaks an answer starts at a forced write

In broken answers, the first token flip that survives in the output comes from a write that bypassed the threshold in 29 of 31 cases on LLaDA and in all 36 on Dream (32 forced writes and 4 block-initial writes, which Dream’s decoder makes once per block without a threshold test). Counting placement flips as well, forced writes carry 99.5% (LLaDA) and 96.7% (Dream) of permanent flips.

(d) Correcting only the forced writes restores the full-precision answers

To test causation, we reran W4A4 on the same questions with one change: at every forced write (on Dream, also at block-initial writes), it used the full-precision choice of position and token for the same state. All other writes stayed quantized, and the decoding schedule was unchanged.

Table R7. Rerunning W4A4 with only its forced writes (on Dream, also its block-initial writes) replaced by the full-precision choice (400 GSM8K questions).

LLaDA-8BDream-7B
Questions broken by quantization3336
… of which answered correctly again30 (91%)32 (89%)
Questions whose outcome differs from full precision, before → after63 → 1263 → 15
Agreement with full precision, before → after84% → 97%84% → 96%

Forced writes are therefore the main channel through which quantization changes answers, and they are the decisions DECAL targets.

(e) Why a near tie can still break an answer

At a near tie either token is often fine locally, which is why most single forced flips are harmless. A tie becomes harmful when it decides how the solution continues: a diffusion model can write any position of the active block, so one forced write can fix the form of the next lines. GSM8K test question 197 shows this (W4A4 without rotation, group size 128, as in Appendix B; Appendix G of the revised PDF gives the full explanation). Both runs first write the identical line “Number of children = 23786 - 8417 - 9092” and its line break, which puts them in the same decoding state. At the next forward pass, no position clears the threshold, so each run writes only its most confident position (boxed; [MASK]: a position not yet written):

position                        97   98      99      100     101     102
before (both runs)    ... 9092  \n   [MASK]  [MASK]  [MASK]  [MASK]  [MASK]  ...
                                     ┌────┐
after: full precision ... 9092  \n   │ \n │  [MASK]  [MASK]  [MASK]  [MASK]  ...
                                     └────┘
                                                             ┌───┐
after: W4A4           ... 9092  \n   [MASK]  [MASK]  [MASK]  │ = │   [MASK]  ...
                                                             └───┘

The two outputs then read:

Full precision

Number of children = 23786 - 8417 - 9092
┌────┐
│ \n │                <- forced write: a second line break (blank line)
└────┘
Now, let's do the subtraction:

23786 - 8417 = 15369
15369 - 9092 = 6277   <- correct

W4A4

Number of children = 23786 - 8417 - 9092
                  ┌───┐
Number of children│ = │23786 - 16419   <- forced write: "=", written first
                  └───┘                   8417 + 9092 is 17509, not 16419
Number of children = 7277              <- wrong (correct: 6277)

Full precision writes a second line break (\n) at position 98 (0.77, against 0.22 for “Number”), leaving a blank line, and then works step by step. W4A4 faces a near tie between two positions, “Number” at position 98 (0.62) and “=” three positions ahead, at position 101 (0.66), and writes the “=” first. This placement flip (Section 3.2), which autoregressive decoding cannot make, fixes the next line as a single equation: the sum 8417 + 9092 is never written out and comes out wrong.

Both continuations are coherent, as the reviewer anticipates, but the W4A4 one moves an addition from the page into the model’s internal computation, which is exactly what quantization degrades. Near-tied choices are therefore not equally safe for a quantized model. This is why risk grows with the number of forced flips (Table R6), and why DECAL weights each position by the reach of its commitment into the rest of the output.

Comments on the paper

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AuthorsOpenReview ↗

Summary of the revision

We thank all reviewers for their constructive feedback. We have uploaded a revised PDF; all changes are shown in blue, and the main text stays within the 10-page limit.

Main text.

  • Introduction: one sentence on how DECAL and the commit temperature divide the work (bXC5).
  • Section 2: Polestar is cited and discussed (An7y).
  • Section 3.2: the share of permanent flips carried by forced commitments now also counts placement flips.
  • Section 4.1: π is stated to serve as a ranking score (An7y, Y31z).
  • Section 4.2: Proposition 1 is noted as a per-state guarantee (An7y).
  • Section 5.1: how the concentration parameter c is set and what it controls (Y31z).
  • Section 5.2: pointer to the Fast-dLLM v2 results (Y31z).
  • Section 5.3 and Table 3: the shuffled control is added, and the claim on the product is softened (all reviewers).

New appendices.

  • G: forced commitments and wrong answers, including the intervention and the example of question 197 (bXC5).
  • H: how DECAL and the commit temperature divide the work (bXC5).
  • I: checks of the flip-probability model (An7y, Y31z).
  • J: drift-guided commitment, as in Polestar (An7y).
  • K: the block-diffusion model Fast-dLLM v2 (Y31z).

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