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Under review as a conference paper at ICLR 2027

Reasoning with Continuous Latent Diffusion

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Abstract

Continuous diffusion generates complete reasoning solutions through iterative refinement in latent space. We introduce Latent Flow Reasoning Models (LFRMs), an ELF-based training and inference recipe. Our experiments show that accurate decoding alone does not ensure effective generation, motivating compact representations learned from multiple layers of a strong autoregressive teacher. Their decomposition also enables asynchronous denoising at different rates. We show that prompt encodings need only preserve the information required for the correct text-conditional score, rather than exactly match teacher features, and use a staged curriculum to learn a compact prompt encoder that replaces the teacher Transformer at inference. We adapt DiffusionNFT to learned self-conditioning guidance and incorporate gold-solution endpoints to supplement sparse rewards. With 90M and 638M denoising backbones, our strongest supervised results outperform reported continuous-diffusion baselines at comparable backbone scales on mathematical reasoning and code generation. NFT further improves single-sample accuracy on math and code, and majority-vote performance on mathematics. Code will be available at: https://anonymous.4open.science/r/LFRM-98B5/.

Primary area:
generative models
Keywords:
continuous diffusion, language model, math, coding

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
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Paper summary

This paper proposes Latent Flow Reasoning Models, which utilize representations from multiple layers of a strong autoregressive teacher. To improve efficiency, the authors also introduce a prompt encoder to replace the teacher Transformer for inference. The authors also adopt asynchronous denoising for different representation components and DiffusionNFT to improve the reasoning ability of the trained models.

Critical strengths
  1. The topic of the paper is interesting. By introducing different layer representations, the authors propose a relatively effective way to utilize continuous latent diffusion for reasoning tasks. The authors also combine different techniques like the asynchronous denoising to improve the performance.
  2. The analyses of different latent representations and prompt encoder training are interesting and provide useful insights.
Critical weaknesses
  1. The generalization of LFRM may be limited. The authors train different models for different tasks instead of a unified model. And there is no generalization evaluation on other types of tasks. Moreover, the fixed 1024-token length limits the maximum sequence length.
  2. The experiments are not comprehensive. Many results are missing in Tables 2 and 3, and different methods are not evaluated under the same settings. Moreover, the method relies on representations from a Qwen3-4B-Instruct teacher, but the authors do not show how using a weaker or stronger teacher model influences performance. Replacing the teacher's prompt representations with the learned encoder also leads to substantial performance degradation on some benchmarks.
Questions for authors
  1. Please see the weaknesses.
  2. Could the authors provide end-to-end inference latency comparisons with existing methods? And what is the cost of building up the training dataset?
9 comments
AuthorsOpenReview ↗

Response to Reviewer MS2M (1/6)

We thank the reviewer for their reading of our paper, and for their questions about generalization, baseline comparability, teacher dependence, and computational cost. We have completed mixed-task adaptation, a smaller-teacher control, additional baseline evaluations, and end-to-end timing measurements. Accuracies below are pass@1 percentages, with generation-seed SD in parentheses.

1. Scientific objective and the cost of teacher replacement

Replacing the teacher's prompt representations with the learned encoder also leads to substantial performance degradation on some benchmarks.

Our objective is competitive continuous-diffusion reasoning with its own compact learned prompt encoder. FMLM+, MLFM, and S-FLM process prompts within their generative systems. Teacher-conditioned ELF variants instead execute an external pretrained contextual encoder during inference, so their accuracy depends on both diffusion and the teacher's contextual computation. A single teacher forward pass may be inexpensive while still supplying powerful semantic features.

Removing that inference-time dependency is a necessary premise of our scientific objective. Training on teacher features is compatible with this goal; at test time, LFRM replaces the contextual Qwen Transformer with the learned prompt encoder, retaining only its frozen vocabulary lookup. This objective holds even when replacement reduces accuracy or the teacher contributes little latency: replacing the teacher is not an attempt to improve the teacher-conditioned system's speed or accuracy.

The performance cost depends strongly on the task. After equal 18-epoch backbone training, GSM8K-B reaches 39.35 (0.59)% with the learned prompt encoder versus 41.05 (0.53)% with the frozen Qwen prompt encoder, using four-seed ODE64 evaluation. Coding shows a larger gap. Holding the epoch-12 denoiser fixed, replacing the frozen Qwen prompt encoder with the MSE-trained prompt encoder reduces HumanEval+ from 30.87 (2.09)% to 25.30 (1.84)%, and MBPP+ from 33.99 (1.62)% to 16.96 (1.11)%. Subsequent joint training and NFT reach 30.18 (1.79)% and 19.61 (1.36)%, respectively, in the existing eight-seed ODE128 evaluation. These later stages adapt both networks.

These experiments quantify the external encoder's contribution: the learned prompt encoder retains most GSM8K accuracy, while MBPP exposes a substantial conditioning bottleneck. Coding's longer, more complex prompts are a plausible explanation (mean training-prefix lengths: 233 tokens versus 84/89 for GSM8K/MATH).

Revised manuscript: Sections 1 and 4.2 explain teacher replacement; Appendix L.2 (Table 33) gives the equal-duration comparison, and Appendix H (Table 24) gives the quoted 128-step coding substitution results; the same appendix also provides prompt-length context.

(cont below)

AuthorsOpenReview ↗

Response to Reviewer MS2M (2/6)

2. Transfer and shared-task modeling

The authors train different models for different tasks instead of a unified model. And there is no generalization evaluation on other types of tasks.

With 64-step DMD2 sampling, the MATH-trained model achieves 36.22% on GSM8K without adaptation and 49.66% after short mixed-task adaptation, keeping MATH500 accuracy near its starting value (28.65% → 28.70%). Before adaptation, our MATH model uses only the math/augmented_math populations of OpenMathInstruct-2, and our GSM8K models use only its gsm8k/augmented_gsm8k populations, alongside Orca-Math and GSM-typed MetaMathQA. Thus the MATH model has not trained on the GSM8K portion of OpenMathInstruct-2, or vice versa.

We present evaluation accuracies using both the standard ODE sampler and a stronger stochastic sampler based on DMD2 (Yin et al., 2024), which interleaves clean-latent prediction and Gaussian noise injection; the precise update rule is specified in Appendix K.1, Eq. (31). Both full benchmarks use four seeds and 64 denoising steps. The headline accuracies above use DMD2.

Before adaptation. The MATH-trained model already transfers substantially to GSM8K, whereas reverse transfer is much weaker, consistent with MATH's greater difficulty. DMD2 evaluations of the supervised epoch-21 LFRM-L models give:

Training taskBackbone/prompt EMAGSM8K evaluationMATH500 evaluation
MATH.9999 / .999936.22 (0.94)28.65 (1.26)
GSM8K.999 / .99964.95 (1.04)4.20 (1.07)

After short mixed-task adaptation. Starting from supervised MATH epoch 21, we jointly fine-tune the backbone and learned prompt encoder for three epochs on 200k GSM8K and 200k MATH training examples, keeping the representation unchanged. Training takes 9.29 H200-hours, approximately 1.6% of the original MATH model's recorded training GPU-hours. For this short adaptation run, we use EMA .999 for both the backbone and prompt encoder: its shorter averaging window tracks recent training updates more quickly than .9999. The GSM8K reverse-transfer reference above uses the same .999/.999 selector; epoch zero retains the actual MATH initialization at .9999/.9999. Each checkpoint is evaluated on both benchmarks:

Mixed-training epochGSM8K, ODEGSM8K, DMD2MATH500, ODEMATH500, DMD2
0: before adaptation22.86 (0.69)36.22 (0.94)21.45 (0.89)28.65 (1.26)
126.84 (0.66)43.20 (1.10)21.00 (2.38)29.40 (1.47)
230.23 (0.90)46.21 (0.38)19.85 (0.57)29.25 (0.30)
333.49 (0.46)49.66 (0.62)19.25 (0.85)28.70 (1.19)

GSM8K accuracy improves at every epoch with both samplers. DMD2 gains 13.44 percentage points, while MATH500 remains near its starting accuracy (28.65% → 28.70%). ODE gains 10.63 points on GSM8K with a 2.20-point MATH500 decrease. The paired DMD2 endpoint differences are +13.44 pp [11.68, 15.22] on GSM8K and +0.05 pp [−2.00, 2.10] on MATH500 (95% problem-bootstrap intervals).

Our coding model already serves both HumanEval and MBPP with one checkpoint, trained on OpenCodeInstruct. Together, these experiments demonstrate shared-checkpoint performance within both mathematical reasoning and coding; unified math-and-code training is a natural next step.

Task-focused training is common among comparable-scale baselines. ELF-REG and S-FLM also train task-specific models, with training budgets comparable to ours (Appendix N.3, Tables 41–42). MLFM covers broader, general-domain tasks, but uses a larger model and a substantially longer reported training budget. FMLM+ and PlaidQ lack sufficient information to report GPU-hours.

Moreover, the fixed 1024-token length limits the maximum sequence length.

The fixed 1,024-token canvas limits the combined prompt-and-answer length. We obtain strong results on the reported benchmarks with a 1,024-token prompt-and-answer canvas; longer canvases or blockwise generation are promising extensions.

Revised manuscript: Appendix L.3 (Table 34, Figure 11) reports mixed-task adaptation, EMA settings, the GSM8K reverse-transfer reference, and additional 32-step results; Section 6.2 uses one coding checkpoint for HumanEval and MBPP. Appendix A.2 documents training populations, and Appendix N.3 (Tables 41–42) gives training scopes and budgets. Appendix K.1, Eq. (31), defines DMD2 sampling.

(cont below)

AuthorsOpenReview ↗

Response to Reviewer MS2M (3/6)

3. Completing and clarifying baseline comparisons

Many results are missing in Tables 2 and 3, and different methods are not evaluated under the same settings.

We have evaluated additional public checkpoints and address comparability along four axes: prompt encoder and training compute, inference cost, scoring, and prompting. The ELF-REG comparisons below use two seeds and supervised LFRM checkpoints, matching the baselines' absence of NFT training.

Additional previously missing entries. The original blanks combined missing evaluations with unavailable task/scale counterparts. In Table 2, S-FLM, FMLM+, ELF-REG-B, and LFRM-B have no MATH-trained checkpoint; our MATH experiments use LFRM-L. In Table 3, FMLM+ has no approximately 650M or MATH-trained counterpart. The revised Tables 2–3 now explain every remaining missing entry beneath the corresponding table, using N/T for absent task/scale counterparts and N/A where denoising NFE does not apply to autoregressive models. The broader appendix comparison separately labels unavailable full-benchmark results as N/R. We added the following evaluations and documented the remaining availability limits:

ModelBenchmark / coverageResult or availability
Qwen3-0.6B-BaseFull MATH50022.40 (2.26)%, official four-shot math-CoT prompt
Qwen3-0.6B thinkingFull GSM8K79.23 (0.43)%, native thinking prompt
MLFM, released checkpointStratified 200-problem MATH500 pilot6/200 correct (3.00%)
MLFM, released checkpointAll 164 HumanEval problems0/164 on base/extended tests, with either naming rule
PlaidQMissing evaluationsOfficial inference code unavailable; author-reported results retained

The MLFM pilot uses seed 42 and its official stochastic/token-promotion sampler; it shows limited transfer from this released checkpoint. Its MATH subset remains separate from full-benchmark comparisons. The Qwen evaluations retain their native AR prompting and generation budgets.

(cont below)

Reviewer_g8h4OpenReview ↗
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Paper summary

This paper introduces Latent Flow Reasoning Models (LFRMs), an ELF-based training and inference recipe for continuous latent diffusion reasoning. It learns compact answer representations from multiple layers of a frozen autoregressive teacher, uses their decomposition for asynchronous denoising, and trains a compact prompt encoder through staged imitation and joint adaptation to replace the teacher Transformer for inference-time conditioning. It also adapts DiffusionNFT to learned self-conditioning guidance and incorporates gold-solution endpoints alongside verifiable rewards. Experiments on mathematical reasoning and code generation report improvements over continuous-diffusion baselines on mathematics and HumanEval, as well as gains after post-training. Representation controls, schedule comparisons, prompt-substitution studies, and theoretical analyses examine aspects of the design, although a substantial MBPP performance gap remains relative to frozen-teacher conditioning.

Critical strengths
  1. The paper demonstrates promising continuous-diffusion reasoning performance. The supervised LFRM models improve over reported continuous-diffusion baselines at comparable denoising-backbone scales on mathematical reasoning and HumanEval code generation, and post-training further improves single-sample performance. Although these comparisons do not establish equal end-to-end computational cost or superiority on every coding benchmark, the results demonstrate a practically interesting direction for non-autoregressive reasoning.

  2. The design is supported by targeted empirical and theoretical analyses. At fixed latent width and teacher prompt conditioning, the single- versus multilayer PCA comparison supports using multiple layers, while the PCA versus learned-multilayer comparison supports learning the projections. Matched schedule comparisons also demonstrate gains from asynchronous denoising. The conditioning lemma and staged prompt-substitution experiments provide a principled motivation for replacing the teacher conditioner. These analyses make the paper more informative than a pipeline evaluated only through final benchmark scores.

Critical weaknesses
  1. The independent contributions of central components remain incompletely isolated, especially in post-training. The representation controls establish a multilayer advantage under PCA and a learning advantage at fixed layers, but omit a learned single-layer control, leaving their interaction unresolved. More importantly, the post-training recipe combines guidance correction and gold-solution anchoring without component ablations or a matched continuation of supervised training on the same gold data. Lemma 2 explains the local anchoring effect, but does not establish its empirical contribution to the complete sampler. Consequently, the pre-/post-NFT gains do not determine how much benefit comes from the proposed reward-based update rather than continued gold-solution supervision. This limits the evidence for the independent benefits of key proposed components.

  2. The practical quality–cost trade-off of compact prompt encoding is insufficiently quantified. The contextual encoder is reduced from approximately 3.63B to 121M parameters, excluding vocabulary maps, and removes the need for the full Qwen Transformer at inference. However, Table 4 shows a persistent MBPP penalty: base accuracy decreases from 38.72% with frozen-Qwen conditioning to 18.45% before NFT and recovers only to 22.26% after NFT. The fixed-backbone prompt-substitution study also confirms a substantial conditioning loss on MBPP. Since prompts are encoded once while generation requires many denoising calls, parameter counts and NFE alone do not establish the overall efficiency benefit. An end-to-end comparison including prompt encoding, denoising, and terminal decoding is needed to assess whether the achieved savings justify this task-dependent loss.

Questions for authors
  1. Evidence needed to isolate the representation contribution: Under the same 1,024-dimensional latent width, frozen teacher prompt conditioning, projection-learning objective, and flow-training protocol, how does a learned single-layer representation compare with the learned multilayer representation? This would clarify whether the multilayer advantage persists beyond the PCA setting and materially affect my assessment of the representation design.

  2. Evidence needed to isolate the post-training contribution: Starting from the same supervised checkpoint, can the authors separate the effects of guidance correction and gold-solution anchoring, and compare with supervised continuation on the same gold data under a reasonably matched optimization budget? For the reward-only control, how would groups without correct generations be handled? These comparisons would materially affect my assessment of the proposed NFT adaptation rather than constitute suggestions for unrelated future work.

  3. Clarification and supporting efficiency evidence: What are the end-to-end latency, throughput, and peak memory of frozen-Qwen versus compact-encoder conditioning under matched hardware, batch size, canvas length, denoising budget, and decoding settings? How do these savings compare with the MBPP accuracy loss? This would materially affect my assessment of the practical benefit of replacing the teacher conditioner.

9 comments
AuthorsOpenReview ↗

Response to Reviewer g8h4 (1/5)

Response to g8h4

We thank the reviewer for their careful reading of our paper, and for their valuable questions and comments that identify the comparisons needed to assess representation design, NFT attribution, and the cost of compact conditioning. We have completed the learned single-layer control, the full NFT component factorial, supervised-continuation controls, and matched end-to-end conditioning measurements. These results directly address the three questions below.

Accuracies below are mean pass@1 percentages, reported as mean (SD).

1. The multilayer advantage persists with learned projectors

The independent contributions of central components remain incompletely isolated, especially in post-training. The representation controls establish a multilayer advantage under PCA and a learning advantage at fixed layers, but omit a learned single-layer control, leaving their interaction unresolved.

Evidence needed to isolate the representation contribution: Under the same 1,024-dimensional latent width, frozen teacher prompt conditioning, projection-learning objective, and flow-training protocol, how does a learned single-layer representation compare with the learned multilayer representation? This would clarify whether the multilayer advantage persists beyond the PCA setting and materially affect my assessment of the representation design.

We added a learned layer-32 control using the same projector-learning objective, 1,024-dimensional latent width, backbone, and flow-training protocol as the learned multilayer model. All four conditions train for six epochs (28,527 optimizer updates).

RepresentationGSM8K pass@1, mean (SD)
PCA single layer 3211.20 (0.56)
Learned single layer 3211.54 (0.61)
PCA multilayer 16/24/3228.43 (0.19)
Learned multilayer 16/24/3230.76 (0.39)

All rows use full GSM8K, four seeds, ODE32, synchronous t=τ2t=\tau^2, CFG1/SCCFG2, and ELF EMA .999. Qwen prompt conditioning is frozen; each condition uses its corresponding representation for both prompt and answer.

Learning the single-layer projector does not close the multilayer gap. Learned multilayer exceeds learned layer 32 by 19.22 pp. Projector learning adds 2.33 pp in the multilayer setting but only 0.34 pp in the single-layer setting.

Revised manuscript: Section 4.1 and Figure 2 include the learned-layer-32 comparison; Appendix C.5 (Tables 12 and 14) gives the four-seed endpoints and learned-layer-32 training curve.

2. NFT gains extend beyond additional gold-solution supervision

More importantly, the post-training recipe combines guidance correction and gold-solution anchoring without component ablations or a matched continuation of supervised training on the same gold data. Lemma 2 explains the local anchoring effect, but does not establish its empirical contribution to the complete sampler. Consequently, the pre-/post-NFT gains do not determine how much benefit comes from the proposed reward-based update rather than continued gold-solution supervision. This limits the evidence for the independent benefits of key proposed components.

Evidence needed to isolate the post-training contribution: Starting from the same supervised checkpoint, can the authors separate the effects of guidance correction and gold-solution anchoring, and compare with supervised continuation on the same gold data under a reasonably matched optimization budget? For the reward-only control, how would groups without correct generations be handled? These comparisons would materially affect my assessment of the proposed NFT adaptation rather than constitute suggestions for unrelated future work.

(cont below)

AuthorsOpenReview ↗

Response to Reviewer g8h4 (2/5)

2.1. Separating guidance correction and gold anchoring

We ran the full factorial over gold endpoints and guidance correction from the same supervised checkpoint. All variants retain joint prompt/backbone updates and the same guided rollout settings. “No guidance correction” means directly optimizing the guided field in the current/old/reference NFT losses, instead of the guidance-corrected field. Rollout and evaluation guidance remain enabled. “No gold endpoints” removes gold solutions from all NFT updates.

NFT variantGold endpointsGuidance correctionUpdate 300Update 600
FullYesYes41.94 (0.94)42.42 (0.63)
Correction onlyNoYes42.42 (0.41)41.60 (1.06)
Gold endpoints onlyYesNo41.49 (0.72)39.44 (0.87)
NeitherNoNo40.88 (1.19)23.56 (0.27)

These are full-GSM8K evaluations with ODE64, async (2.5,2,1.5), CFG1/SCCFG2, and ELF/prompt EMA .99/.99. Both updates use the same four generation seeds (42/123/456/789) for every variant; parentheses give the seed SD.

Three findings clarify attribution. First, removing both components causes pronounced deterioration with longer training, from 40.88% to 23.56%. Second, guidance correction improves accuracy both with and without gold endpoints: at update 600, it adds 2.98 pp with gold endpoints and 18.04 pp without them. Including gold endpoints also substantially buffers deterioration when correction is absent. Third, full NFT has the highest mean at update 600, while correction-only leads at update 300. The gain from adding gold endpoints when correction is already present is modest: 0.82 pp at update 600.

Lemma 2 characterizes the anchoring effect of gold endpoints toward a mixture of the gold posterior target and the old field. Appendix J.1 details the ablations with and without gold endpoints.

2.2. Handling groups without correct generations

This issue arises only in the no-gold ablations. An all-incorrect group receives reward 0 for every sample, so centered advantages are zero and positive/negative NFT weights are equal (ρ=0.5\rho=0.5). Old-field regression and reference regularization can still produce gradients. With gold anchoring, each group has a correct, positive-reward endpoint even when every rollout is incorrect. Filtering of all-correct rollout groups is unchanged; Appendix E.1 specifies the whole-round safeguard.

(cont below)

AuthorsOpenReview ↗

Response to Reviewer g8h4 (3/5)

2.3. Separating NFT from supervised continuation

We compare NFT with two gold-only supervised continuations, both jointly training the backbone and prompt encoder with the original mixed flow/decoder-CE objective and effective batch 512:

  • Standard continuation: resumes the supervised epoch-18 weights and optimizer states at the original learning rate, 0.002.
  • NFT-like continuation: uses NFT's starting weights, learning rate of 0.0001, and fresh optimizer initialization.

Comparison with NFT at 300 updates.

MethodUpdatesEstimated EFLOPsAccuracy (SD), %Comparison
Full NFT3002.1341.94 (0.94)Reference
Standard continuation3000.1939.03 (0.29)Matched updates
NFT-like continuation3000.1938.50 (0.77)Matched updates
Standard continuation6,0003.7839.95 (1.07)Matched compute
NFT-like continuation6,0003.7837.76 (0.66)Matched compute

Comparison with NFT at 600 updates.

MethodUpdatesEstimated EFLOPsAccuracy (SD), %Comparison
Full NFT6004.1542.42 (0.63)Reference
Standard continuation6000.3839.31 (0.26)Matched updates
NFT-like continuation6000.3838.23 (0.70)Matched updates
Standard continuation8,0005.0440.03 (0.73)Matched compute
NFT-like continuation8,0005.0437.68 (0.49)Matched compute

Both tables report mean pass@1 (generation-seed SD) over seeds 42/123/456/789 on all 1,319 GSM8K test problems, using ODE64, async (2.5,2,1.5), and CFG1/SCCFG2. Evaluation uses ELF/prompt EMA .9999/.9999 for supervised continuation and .99/.99 for NFT. The compute-matched controls use 6,000/8,000 supervised updates for comparison with NFT at 300/600 updates, with compute budgets that meet or exceed NFT's compute; the exact FLOPs are shown above. Appendix J.2 gives the initialization and compute-accounting details.

We report EMA .9999 for supervised continuation because it consistently outperformed .99 in our matched EMA comparisons. For the NFT-like continuation, this holds at both 300 and 6,000 updates; using .99 would increase NFT's measured advantage. Appendix J.2 provides the comparison.

NFT's gain persists beyond additional gold supervision. NFT outperforms both supervised continuations in the update-matched and compute-matched comparisons. At update 600, full NFT exceeds standard continuation at 8,000 updates by 2.39 pp, despite the continuation receiving approximately 21.5% more compute. NFT without gold endpoints also exceeds that control by 1.57 pp, further supporting a benefit from reward-based learning beyond additional gold supervision.

Compute estimates include NFT rollouts, including discarded generations, training forwards/backwards, prompt computation, and optimizer matrix operations.

Guidance correction and gold endpoints modify training without adding inference modules or denoiser calls.

2.4. Uncertainty in the accuracy improvements

We resample test problems 4,000 times, keeping the four generation seeds together within each problem and pairing the compared methods (95% percentile intervals).

Component effects at update 600 (ODE64). Each comparison changes one component while holding the other fixed.

Effect being measuredOther componentComparisonDifference, ppPaired 95% interval
Guidance correctionGold presentFull − Gold endpoints only+2.98[1.84, 4.15]
Guidance correctionGold absentCorrection only − Neither+18.04[16.36, 19.66]
Gold endpointsCorrection presentFull − Correction only+0.82[−0.08, 1.74]
Gold endpointsCorrection absentGold endpoints only − Neither+15.88[14.35, 17.38]

Comparisons with supervised continuation (ODE64). Full NFT at update 600 is compared with each continuation at 8,000 updates.

ComparisonDifference, ppPaired 95% interval
Full NFT − standard continuation (8,000 updates)+2.39[1.25, 3.54]
Full NFT − NFT-like continuation (8,000 updates)+4.74[3.54, 5.91]

Revised manuscript: Section 6.1 (Table 4) presents the component ablations and both supervised-continuation controls. Appendix J.1 describes gold removal, guided-field optimization, and all-incorrect groups; Appendix J.2 (Table 28) gives compute and paired comparisons. Appendix E.1 specifies the whole-round safeguard. The anchoring analysis is in Section 5.2 (Lemma 2) and Appendix E.4.

(cont below)

Reviewer_5A9SOpenReview ↗
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Paper summary

This paper introduces Latent Flow Reasoning Models (LFRMs), which builds upon Embedded Language Flows (ELF; Hu et al.) by learning representations from teacher-forced Qwen3-4B-Instruct-2507 activations. Additionally, the teacher is replaced at inference time with a compact prompt encoder. To allow for this, the flow model is frozen after training for 12 epochs so that the compact encoder can be learned before unfreezing the flow model and training it jointly with the encoder in the final stage. Because the framework uses a multilayer representation, the authors choose to use layer-specific "clocks" to schedule the denoising for each feature group.

The authors adapt Diffusion-NFT for reinforcement learning and train two models which they evaluate on math and code.

Critical strengths

None

Critical weaknesses
  • This paper is incredibly hard to read
  • There appear to be no properly matched baselines
Questions for authors
  • Is the training data and setting the same for the ELF-REG models as the LFRM? If not, can you match this and share the results for comparison?
  • How is the performance on MATH500 for backbones below 200M?
  • In Table 4, what exactly is the frozen-Qwen setting? What are the ELF performances on HE and MBPP?
4 comments
AuthorsOpenReview ↗

Response to Reviewer 5A9S (1/4)

We address the training-data and baseline comparisons, the model scales studied, and the frozen-Qwen coding setting below. New accuracy measurements are mean pass@1 percentages with generation-seed SD in parentheses. External comparisons use two seeds, 42/123, and supervised LFRM checkpoints, without NFT.

1. Training data, compute, and matched comparisons

Is the training data and setting the same for the ELF-REG models as the LFRM? If not, can you match this and share the results for comparison?

1.1. Training data

LFRM and ELF-REG use substantially overlapping source corpora, but different final training populations. The sources are:

TaskLFRMELF-REG
GSM8KGSM-derived OpenMathInstruct-2, MetaMathQA, and Orca-MathGSM-derived OpenMathInstruct-2 and MetaMathQA
MATHMATH-derived OpenMathInstruct-2MATH-derived OpenMathInstruct-2
CodeOpenCodeInstructOpenCodeInstruct

Filtering and held-out populations differ. The submitted Appendix A describes our training data; ELF-REG describes its construction in Appendix B.2.

We note that ELF-REG is concurrent work, first submitted to arXiv on September 24, 2026. We do not consider fully retraining concurrent ELF-REG on an identical final training population a reasonable requirement for assessing this paper. The relevant evidence includes comparisons against released models and controlled experiments isolating our proposed design choices; we provide both.

We do assess competitiveness using released ELF-REG checkpoints and the authors’ reported results, with training populations, teacher resources, and costs documented explicitly. To isolate our design contributions, we additionally conduct controlled experiments holding the data, teacher, backbone, optimization budget, and prompt representations fixed.

There appear to be no properly matched baselines

The original submission already included comparisons at comparable backbone sizes and denoising budgets (Tables 2–3), coding comparisons under both standard and ELF-REG’s function-name-aliasing scoring (Table 4; Appendix H, Table 18), and representation controls with matched data and training budgets (Figure 2). The revised experiments strengthen these existing comparisons through common-prompt evaluations, explicit training-cost accounting, and fixed-prompt controls.

We address matching along four axes: prompt encoder and training compute, inference cost, scoring, and prompting. We additionally provide controlled representation comparisons that hold data, teacher, backbone, training budget, and prompt tensors fixed.

1.2. Prompt encoder and training compute

Our teacher-conditioned epoch-12 checkpoints outperform ELF-REG on all evaluated tasks, including coding, with fewer model-training H200-hours. These checkpoints retain teacher prompt conditioning, providing the closest comparison to ELF-REG's conditioning setup. The mathematical results below include both published scores and evaluations using identical rendered prompts and scorers; the coding comparison appears below under “Frozen-Qwen conditioning and coding comparisons.”

Benchmark / scaleELF-REG, author-reportedELF-REG, common prompts/scorersLFRM epoch 12, frozen QwenLFRM final supervised, learned encoder
GSM8K / B38.1135.90 (0.48)39.65 (0.75)39.27 (0.54)
GSM8K / L55.9653.94 (1.45)61.94 (1.07)59.02 (0.70)
MATH500 / L13.3912.70 (0.14)18.70 (0.42)21.50 (1.27)

Both LFRM conditioning variants exceed the corresponding author-reported ELF-REG scores. LFRM uses ODE64; ELF-REG uses its released ODE configuration with 63 denoising calls for GSM8K and 127 for MATH500. Each adds one terminal decoding call and retains its established guidance settings. Our frozen contextual encoder is Qwen-4B; ELF-REG uses Qwen-0.6B, with a separate Qwen-1.7B alignment teacher during training.

Task / scaleLFRM epoch 12 (H200-hours)LFRM final pre-NFT checkpoint (H200-hours)ELF-REG reported H200-hours
GSM8K / B≈42.1≈63.7 (epoch 18)156.5
GSM8K / L≈200.4≈352.0 (epoch 21)333.9
MATH / L≈330.5≈594.6 (epoch 21)563.1
Coding / L≈404.5≈478.4 (epoch 13)407.9

Training hours are reconstructed from recorded training logs and allocation records. Final pre-NFT totals include prompt adaptation. ELF-REG times come from Table 7, including GSM8K initialization for MATH. Epoch 12 provides the appropriate teacher-conditioned comparison. Training after epoch 12 primarily adapts LFRM to its compact learned prompt encoder, an additional objective ELF-REG does not undertake.

(cont below)

AuthorsOpenReview ↗

Response to Reviewer 5A9S (2/4)

1.3. Inference cost

We measured end-to-end generation on one H200 using the same 32 GSM8K questions and three warmed repeats, including prompt encoding and terminal decoding. LFRM has lower single-request latency and comparable batch throughput to ELF-REG at both backbone scales:

  • B scale: LFRM / ELF-REG take 501.6 / 530.5 ms per request, with 9.77 / 9.57 problems/s at batch 32.
  • L scale: LFRM / ELF-REG take 1,255.5 / 1,285.9 ms, with 1.48 / 1.49 problems/s at batch 32.

These use 64 LFRM versus 63 ELF-REG denoising calls, followed by one terminal decoding call, with uncompiled native inference for both. Appendix N.1, Tables 38–39, gives the measurements and timing-repeat SDs.

1.4. Scoring

The mathematical comparisons use identical numerical-answer scoring for GSM8K and Math-Verify for MATH500. Coding comparisons use identical EvalPlus benchmark versions, sanitization, execution limits, and full base/extended tests. We separately apply standard scoring and ELF-REG's single-function name-aliasing rule to the same generations; Section 3 below gives both comparisons. This separation matters because function-name repair changes the MBPP ordering.

1.5. Prompting

For mathematics, we evaluated ELF-REG using LFRM's exact rendered prompts and token IDs; Section 1.2 also retains the stronger author-reported scores. For code, ELF-REG uses a plain completion prompt ending in Python solution:, whereas LFRM uses Qwen's user/assistant chat format. Replacing ELF-REG's native wrapper with our exact prompt, while keeping its checkpoint, sampler, and scoring fixed, reduced standard HumanEval/MBPP+ accuracy from 24.09/21.43% to 3.66/2.38%. We therefore use its stronger native-prompt results in the principal coding comparison and report the common-prompt experiment separately in Appendix M.3, Table 37.

1.6. Controlled comparisons additionally fix the training resources

We train the same LFRM-B initialization for six epochs with identical data, Qwen teacher, 1,024-token canvas, 1,024-dimensional latent width, optimization batch, and flow/decoder objective. Holding the prompt tensors identical isolates the answer representation:

Answer representation, identical learned-multilayer prompt encodingGSM8K pass@1
PCA layer 3214.06 (0.19)
Learned layer 3212.57 (0.81)
PCA layers 16/24/3228.58 (1.39)
Learned layers 16/24/3230.76 (0.39)

These use four seeds, ODE32, synchronous squared clocks, and SCCFG2. They establish that the representation improvements persist with training resources and prompt conditioning controlled. Together, the external comparisons demonstrate the competitiveness of the complete recipe, while the controlled experiments establish the benefits of our representation design.


Regarding the reviewer’s broader criticism that

There appear to be no properly matched baselines

we respectfully ask the reviewer to identify which comparisons in the original submission or added in our rebuttal they consider improperly matched, and which uncontrolled factors undermine those comparisons. As detailed above, the original submission already included comparisons at comparable model scales and denoising budgets, matched coding-scoring comparisons, and representation controls with matched data and training budgets.

Revised manuscript: Appendix A.2 (Table 8) documents training populations; Appendices M.1–M.3 (Tables 35–37) separate common-prompt mathematics, native-prompt coding under both scoring rules, and prompt-format sensitivity. Appendices N.1 and N.3 give inference costs (Tables 38–39) and training budgets (Tables 41–42). The controlled fixed-prompt comparison appears in Appendix C.5 (Table 13).

(cont below)

AuthorsOpenReview ↗

Response to Reviewer 5A9S (3/4)

2. Backbone sizes studied

How is the performance on MATH500 for backbones below 200M?

Our sub-200M experiments study GSM8K; MATH500 and code are evaluated with the larger backbone, matching the scale of the available baseline comparisons.

Revised manuscript: Sections 6.1–6.2 (Tables 2, 3, and 5) and Appendix M.4 specify benchmark/model coverage; Appendix A.1 (Table 6) gives the architectures.

3. Frozen-Qwen conditioning and coding comparisons

In Table 4, what exactly is the frozen-Qwen setting? What are the ELF performances on HE and MBPP?

Frozen-Qwen means that our epoch-12 diffusion backbone receives question-only contextual representations from frozen Qwen; the answer starts from Gaussian noise and is generated by diffusion. The submitted draft defines this in Section 4.2 (p. 5, lines 250–252): “Train the flow model for 12 epochs using fixed Qwen prompt representations and the flow/decoder objective.” Its Table 4 caption (p. 9, line 469) explicitly labels “Frozen Qwen: epoch 12.” The subsequent learned-prompt rows replace the contextual teacher with our compact encoder and include further joint training.

The original ELF paper trained on OpenWebText, WMT14, and XSum, and did not train a coding model. ELF-REG was trained on code, and we evaluate its released coding checkpoint below.

For ELF-REG, the submitted Section 6.2 (p. 9, lines 481–482) already states: “Under matched function-name aliasing, they also exceed ELF-REG-L (Appendix H).” The comparison is in Appendix H, Table 18 (p. 39). Appendix H (p. 38, lines 2044–2049) explains its separation from the main table: “Mixing repaired and unrepaired scores would therefore obscure a substantial difference in acceptance criteria.” ELF-REG's reported scores allow function-name repair, whereas the main coding table uses standard scoring without repair. We now evaluate its released checkpoint under both protocols so the comparison is explicit.

All rows below use identical EvalPlus benchmark versions, sanitization, execution limits, and base/extended tests, with each model's native prompt. HumanEval contains 164 problems; both MBPP columns contain the same 378 problems. Parentheses give two-seed SDs.

3.1. Standard scoring, without function-name repair

Model / prompt encoderHumanEvalHumanEval+MBPP-378 baseMBPP+ extended
ELF-REG-L / frozen Qwen-0.6B24.09 (0.43)23.17 (0.00)24.60 (1.87)21.43 (1.12)
LFRM-L / frozen Qwen-4B35.06 (0.43)32.62 (0.43)39.81 (0.94)34.26 (0.19)
LFRM-L / learned prompt encoder32.01 (3.02)28.66 (0.86)19.58 (1.50)17.33 (1.68)

LFRM uses 128 denoising calls and ELF-REG uses 127, with one terminal decoding call for each. LFRM with the frozen Qwen prompt encoder leads on all four metrics. LFRM with the learned prompt encoder outperforms ELF-REG on HumanEval(+), while ELF-REG leads on standard-scoring MBPP.

3.2. Single-function aliasing, as used by ELF-REG

Model / prompt encoderHumanEvalHumanEval+MBPP-378 baseMBPP+ extended
ELF-REG-L / frozen Qwen-0.6B24.70 (0.43)23.78 (0.86)29.50 (2.06)25.53 (1.31)
LFRM-L / frozen Qwen-4B35.06 (0.43)32.62 (0.43)44.84 (0.56)38.23 (0.56)
LFRM-L / learned prompt encoder32.01 (3.02)28.66 (0.86)32.94 (0.19)29.10 (0.37)

This table rescores the same native-prompt generations under identical single-function alias rules and tests. Under this protocol, both supervised LFRM variants outperform ELF-REG on all four metrics. The naming rule changes the MBPP ordering, making its explicit separation important for interpreting comparisons. The stronger frozen-Qwen results also show why removing an external prompt teacher is a substantive modeling challenge: teacher-conditioned accuracy reflects both the diffusion model and the external contextual encoder.

Revised manuscript: Section 4.2, Section 6.2 (Table 5), and Appendix A.2 define the frozen-Qwen stage and subsequent adaptation. Appendix M.2 (Table 36) separates standard and alias scoring for ELF-REG/LFRM; Appendix M.3 (Table 37) isolates prompt-format sensitivity. Appendix H gives the coding protocol and stage results.

(cont below)

AuthorsOpenReview ↗

Response to Reviewer 5A9S (4/4)

4. Readability and presentation

This paper is incredibly hard to read

We have revised the exposition and navigation to make the method and evidence easier to follow:

  • Purpose and structure: Section 1 clarifies the scientific objective and contributions; Section 4 now opens with a roadmap connecting representation learning, prompt conditioning, inference, and reinforcement learning.
  • Ablations: Sections 4.1–4.2 use finding-oriented headings and explain what each comparison holds fixed and what it shows. Section 6.1 separates NFT component ablations from supervised-continuation controls.
  • Figures and tables: Figure 3 now explains frozen-Qwen conditioning, the encoder replacement, subsequent joint training, and the sampling setup. Tables 2–3 explain N/A and N/T entries, and Table 5 explains the unavailable PlaidQ evaluation.
  • Appendix navigation: A linked contents page lists appendix sections and subsections with page numbers, making settings, proofs, protocols, and additional results directly accessible.

Revised manuscript: Section 1; the Section 4 roadmap and Sections 4.1–4.2; Figure 3; Section 6.1 and Tables 2–5; the appendix contents page. Appendices M–N group additional evaluation protocols and resource measurements separately.

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

This paper introduces Latent Flow Reasoning Models (LFRMs), an ELF-based approach to generating reasoning solutions through continuous latent denoising. The method combines learned projections of multiple layers of a frozen autoregressive teacher, a staged procedure for replacing teacher-based prompt conditioning with a compact encoder, inference-time asynchronous denoising across representation groups, and a guidance-compatible adaptation of DiffusionNFT incorporating gold-solution endpoints. Two lemmas characterize information preservation under prompt encoding and the local anchoring effect of gold endpoints. Experiments on GSM8K, MATH500, HumanEval, and MBPP demonstrate competitive results against reported continuous-diffusion baselines and improved single-sample accuracy after NFT.

Critical strengths
  1. A useful empirical investigation of representations for continuous reasoning generation. The paper studies an important design choice beyond the denoising architecture itself. In Table 10, multilayer PCA substantially outperforms single-layer PCA, and learned multilayer projections provide an additional improvement. The clean-token reconstruction probe also usefully distinguishes recoverability of tokens from clean representations from successful generation through denoising. These findings provide actionable evidence for developing continuous reasoning models, although their precise attribution requires further controls.

  2. A working end-to-end recipe with consistent single-sample post-training gains and transparent reporting. LFRM-L improves from 58.67% to 63.74% on GSM8K and from 21.18% to 24.68% on MATH500 after NFT at the reported headline settings. Coding results also improve after NFT. The appendices carefully distinguish sampling variation from training variation, standard code evaluation from function-name repair, and oracle coverage from majority voting. This transparency strengthens the empirical contribution and makes its limitations assessable.

Critical weaknesses
  1. The experiments do not sufficiently isolate the contributions central to the proposed recipe. The representation construction is used for both answer targets and teacher prompt conditions (Appendix A), while Appendix C.4 does not clearly establish that the actual prompt representations remain identical across the representation ablations. If both change, Figure 2 cannot isolate the effect of the answer latent space. More importantly, NFT combines reward-based updates with gold endpoints, preferential rewards for gold solutions, guidance correction, and joint encoder updates, but lacks controls separating these effects. An equal-update gold-only continuation and NFT variants without gold endpoints or guidance correction would be particularly informative. Lemma 2 explains the local regression anchor but does not establish that the proposed combination improves upon simpler supervised continuation. Consequently, the results demonstrate that the complete procedure helps, but leave substantial uncertainty about which proposed mechanisms account for the gains.

  2. The practical advantage of the compact conditioning and inference design remains insufficiently established. The compact encoder removes the teacher Transformer from inference, but entails additional training and sometimes substantial accuracy loss. In Table 4, MBPP+ falls from 33.99% with frozen-Qwen conditioning to 16.40% before NFT and recovers only to 19.61% afterward. Mathematical comparisons also lack a teacher-conditioned continuation trained for the same total duration. Meanwhile, the incremental benefit of asynchronous inference is setting-dependent: Appendix D.2 reports a MATH500 improvement of only 0.50 points at 32 steps, with a confidence interval crossing zero, and a negative point estimate at 16 steps. External comparisons use different training and evaluation protocols, and denoising NFE excludes prompt encoding and terminal decoding. Although these limitations are acknowledged, the absence of end-to-end latency and training-cost measurements makes it difficult to assess whether the additional machinery delivers a compelling performance–cost trade-off.

  3. This paper’s distinct methodological novelty is not sufficiently clear. The proposed framework combines representation learning, staged encoder adaptation, asynchronous denoising, and reward-based fine-tuning, but the presentation does not clearly distinguish its original advances from adaptations of established ideas. Although the empirical improvements support the usefulness of the overall recipe, they do not establish what new principle or mechanism the paper contributes beyond extending these ideas to reasoning tasks. The authors should clarify the central innovation, identify the specific technical obstacle that existing approaches cannot adequately address, and explain how the proposed design overcomes it.

Questions for authors
  1. Clarification concerning representation attribution: Are the prompt-condition tensors identical across the single-layer PCA, multilayer PCA, and learned multilayer experiments in Figure 2? If not, is there evidence from a fixed-prompt-condition comparison that isolates changes to the answer representation?

  2. Evidence concerning post-training attribution: What evidence distinguishes the benefits of reward-based NFT from additional gold-solution supervision? Results for an equal-update gold-only continuation, NFT without gold endpoints, and NFT without SCCFG correction would materially affect my assessment. Please distinguish available results from experiments that have not been conducted.

  3. Could the authors supplement the evaluation with direct, controlled baselines that test the proposed additions? The most informative comparisons would be:

  1. A basic ELF model trained with the same data, teacher resources, and comparable training budget, to separate improvements from differences in supervision and computational investment.
  2. Representation ablations that keep the prompt-condition tensors identical while changing only the answer representation, to isolate the benefit of the proposed latent space.
  3. An equal-update gold-only supervised continuation, together with NFT variants without gold endpoints and without SCCFG correction, to distinguish additional supervision from reward-based learning and the proposed guidance adaptation. These comparisons would materially affect my assessment by identifying which components explain the reported gains. If a full set is infeasible, could the authors prioritize a matched ELF baseline and the gold-only continuation, and clarify which remaining comparisons are already available?
8 comments
AuthorsOpenReview ↗

Response to Reviewer WJDV (1/7)

We thank the reviewer for their careful reading of our paper, and for their valuable questions and comments that identify the controls needed to distinguish answer-representation design, prompt conditioning, and post-training effects. We have completed additional training and evaluations addressing these questions, including fixed-prompt representation controls, a learned single-layer control, a gold-endpoint × guidance-correction factorial, and two supervised-continuation controls.

Accuracies below are mean pass@1 percentages, reported as mean (SD).

1. Scientific objective: reasoning without an external prompt teacher

The practical advantage of the compact conditioning and inference design remains insufficiently established.

Our objective is to establish competitive reasoning with a continuous-diffusion model and its own compact conditioning network. FMLM+, MLFM, and S-FLM process prompts within their generative systems. In contrast, teacher-conditioned ELF variants execute an external pretrained contextual encoder during inference. Their accuracy therefore depends on both the diffusion model and the teacher's contextual computation. A single teacher forward pass may be inexpensive while still supplying powerful semantic features.

Removing that inference-time dependency is a necessary premise of our scientific objective: can latent diffusion models achieve strong performance on reasoning tasks, without invoking a powerful external context encoder model at inference time? Using the teacher to construct training representations or initialize a learned conditioner is compatible with this goal; continuing to call it at test time leaves the external contextual computation in the reasoning system. Consequently, replacing the teacher is not an attempt to improve the teacher-conditioned system's latency or accuracy. A small runtime contribution, or a loss of accuracy on replacement, does not resolve the scientific question. We replace the contextual Qwen Transformer while retaining its frozen vocabulary lookup.

Revised manuscript: Sections 1 and 4.2 explain the scientific objective and the role of learned prompt conditioning.

We address the three comparisons identified as most informative in the order listed, followed by conditioning and inference trade-offs, technical contributions, and a component-cost summary.

2. A controlled single-layer ELF-style reference

  1. A basic ELF model trained with the same data, teacher resources, and comparable training budget, to separate improvements from differences in supervision and computational investment.

Controlled single-layer references. Original ELF uses the final T5 encoder layer. To match LFRM's data, teacher resources, and 1,024-dimensional denoising space, we train two ELF-style references using Qwen layer 32: one with PCA projection and one with projection learned through decoding CE. Both retain our ELF-B backbone, 1,024-token canvas, and training objective.

RepresentationGSM8K accuracy, mean (SD)Estimated denoiser training (EFLOPs)
ELF-style Single-layer PCA: Qwen 32 → 1,02411.20% (0.56)17.24
ELF-style Single-layer learned: Qwen 32 → 1,02411.54% (0.61)17.24
Learned multilayer: Qwen 16/24/32 → 256/256/51230.76% (0.39)17.24

All rows use frozen Qwen conditioning in the corresponding prompt/answer representation, ELF EMA .999, ODE32 with the shared-square clock, CFG1/SCCFG2, and four generation seeds. FLOPs are estimated from profiled training operations; representation preparation is excluded.

We highlight the following comparisons:

  1. Matched training budget. Both references and our learned multilayer model train for six epochs (28,527 optimizer updates), matching the optimization budget and denoiser workload. The table reports their common estimated denoiser-training FLOPs.

  2. A substantial multilayer advantage. Learned multilayer achieves 30.76%, exceeding single-layer PCA and learned projection by 19.56 and 19.22 percentage points, respectively, at comparable training cost.

  3. External conditioning remains a separate limitation. These ELF-style references still call the external Qwen encoder at inference, falling short of our scientific objective of strong continuous-diffusion reasoning without an external contextual encoder.

Revised manuscript: Section 4.1 (Figure 2) discusses the single-layer controls; Appendix C.5 (Tables 12–14) records endpoints, fixed-prompt controls, and their learning curves.

(cont below)

AuthorsOpenReview ↗

Response to Reviewer WJDV (2/7)

3. Answer-representation gains with identical prompt conditions

The experiments do not sufficiently isolate the contributions central to the proposed recipe. The representation construction is used for both answer targets and teacher prompt conditions (Appendix A), while Appendix C.4 does not clearly establish that the actual prompt representations remain identical across the representation ablations. If both change, Figure 2 cannot isolate the effect of the answer latent space.

Clarification concerning representation attribution: Are the prompt-condition tensors identical across the single-layer PCA, multilayer PCA, and learned multilayer experiments in Figure 2? If not, is there evidence from a fixed-prompt-condition comparison that isolates changes to the answer representation?

Representation ablations that keep the prompt-condition tensors identical while changing only the answer representation, to isolate the benefit of the proposed latent space.

The original Figure 2 used the same representation construction for prompt and answer, so the prompt tensors were indeed not identical across its variants. Sharing the prompt/answer representations provides a simple conditioning interface, but the reviewer is correct that this comparison alone does not isolate the answer space.

We therefore trained new controls which all use identical learned-multilayer prompt representations, changing only the answer representation. We chose the learned 16/24/32 representation for this fixed prompt because it was the strongest representation in the original matched ablations. The controls retain the same ELF-B initialization, training data and order, 1,024-dimensional latent width, six-epoch training budget, objective, and optimization settings.

Answer representationOriginal: matching prompt representationFixed learned-multilayer promptChange (pp)
Learned multilayer30.76 (0.39)30.76 (0.39), reused reference0.00
PCA multilayer28.43 (0.19)28.58 (1.39)+0.15
PCA layer 3211.20 (0.56)14.06 (0.19)+2.86
Learned layer 3211.54 (0.61)12.57 (0.81)+1.02

Evaluations match the existing representation ablations. The learned-multilayer reference is reused because it already satisfies the fixed-prompt condition.

The multilayer advantage persists after controlling prompt encoding. With prompt tensors fixed, learned multilayer exceeds PCA multilayer by 2.18 pp and learned layer 32 by 18.20 pp; PCA multilayer exceeds PCA layer 32 by 14.52 pp. The learned single-layer result changes from 11.54% to 12.57%, leaving the large gap to learned multilayer. Learning the projector improves the multilayer representation; the learned single-layer control remains below single-layer PCA. Together, these controls separate answer-representation gains from changes in prompt conditioning.

Revised manuscript: Section 4.1 and Figure 2 present the representation comparison with matching and fixed prompt encoding; Appendix C.5 (Tables 12–13) gives the four-seed endpoints under both conventions.

(cont below)

AuthorsOpenReview ↗

Response to Reviewer WJDV (3/7)

4. Supervised continuation and NFT component ablations

More importantly, NFT combines reward-based updates with gold endpoints, preferential rewards for gold solutions, guidance correction, and joint encoder updates, but lacks controls separating these effects. An equal-update gold-only continuation and NFT variants without gold endpoints or guidance correction would be particularly informative. Lemma 2 explains the local regression anchor but does not establish that the proposed combination improves upon simpler supervised continuation. Consequently, the results demonstrate that the complete procedure helps, but leave substantial uncertainty about which proposed mechanisms account for the gains.

Evidence concerning post-training attribution: What evidence distinguishes the benefits of reward-based NFT from additional gold-solution supervision? Results for an equal-update gold-only continuation, NFT without gold endpoints, and NFT without SCCFG correction would materially affect my assessment. Please distinguish available results from experiments that have not been conducted.

An equal-update gold-only supervised continuation, together with NFT variants without gold endpoints and without SCCFG correction, to distinguish additional supervision from reward-based learning and the proposed guidance adaptation. These comparisons would materially affect my assessment by identifying which components explain the reported gains. If a full set is infeasible, could the authors prioritize a matched ELF baseline and the gold-only continuation, and clarify which remaining comparisons are already available?

4.1. Separating the two NFT modifications

We ran the full factorial over gold endpoints and guidance correction from the same supervised checkpoint. All variants retain joint prompt/backbone updates and the same guided rollout settings. “No guidance correction” means directly optimizing the guided field in the current/old/reference NFT losses, instead of the guidance-corrected field. Rollout and evaluation guidance remain enabled. “No gold endpoints” removes gold solutions from all NFT updates.

NFT variantGold endpointsGuidance correctionUpdate 300Update 600
FullYesYes41.94 (0.94)42.42 (0.63)
Correction onlyNoYes42.42 (0.41)41.60 (1.06)
Gold endpoints onlyYesNo41.49 (0.72)39.44 (0.87)
NeitherNoNo40.88 (1.19)23.56 (0.27)

These are full-GSM8K evaluations with ODE64, async (2.5,2,1.5), CFG1/SCCFG2, and ELF/prompt EMA .99/.99. Both updates use the same four generation seeds (42/123/456/789) for every variant; parentheses give the seed SD.

Three findings clarify attribution. First, removing both components causes pronounced deterioration with longer training, from 40.88% to 23.56%. Second, guidance correction improves accuracy both with and without gold endpoints: at update 600, it adds 2.98 pp with gold endpoints and 18.04 pp without them. Including gold endpoints also substantially buffers deterioration when correction is absent. Third, full NFT has the highest mean at update 600, while correction-only leads at update 300. The gain from adding gold endpoints when correction is already present is modest: 0.82 pp at update 600.

Lemma 2 characterizes the anchoring effect of gold endpoints toward a mixture of the gold posterior target and the old field. Appendix J.1 details the ablations with and without gold endpoints.

(cont below)

Comments on the paper

3 comments
AuthorsOpenReview ↗

Global Response (1/3)

We thank the reviewers for the discussion and for their valuable suggestions. Following our responses and additional experiments, WJDV and MS2M raised their ratings to weak acceptance. We incorporated the new experiments and clarifications into the revised manuscript. Below, we first summarize our contributions, followed by a summary of common issues raised by reviewers.

Summary of contributions

Our central contribution is a pipeline for strong continuous latent-diffusion reasoning without an external prompt encoder at inference. Its stages establish a strong denoiser, make it independent of the teacher, and enable further improvement through diffusion RL:

  1. Learning multilayer representations that support strong downstream reasoning.

    • We learn a compact latent representation by projecting multiple AR-teacher layers, with projectors trained using downstream decoding cross-entropy. Controlled ablations establish three findings:

      • Multilayer representations outperform single-layer alternatives.
      • Learned multilayer projectors outperform PCA projectors.
      • In matched training experiments, Qwen-4B representations yield higher reasoning accuracy than Qwen-0.6B representations.
    • The same representation decomposition enables flexible asynchronous inference: different layer components follow different denoising clocks. Our comparisons show gains over synchronous inference with both deterministic and stochastic samplers, without needing additional training, and with essentially the same inference cost.

    WJDV recognized the representation findings as providing “actionable evidence for developing continuous reasoning models.” MS2M likewise highlighted the analyses of latent representations and prompt-encoder training as providing “useful insights.”

  2. Staged prompt learning makes the resulting model independent of the AR teacher at inference.

    • We replace the external teacher prompt encoder with a compact learned prompt encoder. The resulting model's strong performance answers a key scientific question: can latent diffusion achieve strong reasoning performance without relying on a powerful external pretrained prompt encoder at inference? This also enables fair comparison with FMLM+, MLFM, and S-FLM, which likewise do not invoke an external prompt encoder.
    • Our theory shows that preserving the relevant conditioning information suffices to recover the full-prompt conditional score, without exactly matching teacher prompt features.
    • Ablations show that joint learning from initialization performs poorly; our staged curriculum first trains the denoiser, then fits the prompt encoder and adapts both jointly.

    g8h4 noted that the conditioning lemma and staged prompt-substitution experiments “provide a principled motivation for replacing the teacher conditioner.”

  3. Guidance-corrected DiffusionNFT further improves reasoning through post-training RL.

    • We adapt DiffusionNFT to be compatible with our model's learned self-guidance, retaining guided rollouts while correcting the optimized field. Ablations establish the importance of this correction.
    • Gold solutions provide an additional regularization anchor. We theoretically characterize and empirically validate this effect.
    • NFT improves accuracy across math and coding tasks. On GSM8K, guidance-corrected NFT outperforms both supervised-continuation controls, even without gold endpoints.
  4. The complete pipeline delivers strong reasoning performance both before and after NFT.

    • With DMD2-based stochastic sampling, pre-NFT LFRM outperforms all compared continuous-diffusion baselines at comparable backbone scales on math and code.
    • With deterministic ODE sampling, pre-NFT LFRM also outperforms these baselines on math and HumanEval; NFT further improves ODE accuracy on math and code.
    • We additionally quantify training and inference costs under the matched comparisons.

    WJDV recognized a “working end-to-end recipe with consistent single-sample post-training gains and transparent reporting,” while g8h4 highlighted “promising continuous-diffusion reasoning performance.”

AuthorsOpenReview ↗

Global Response (2/3)

Common Issues Raised

Common issue 1: The accuracy cost and scientific purpose of replacing the prompt teacher. (WJDV, g8h4, MS2M)

  • Prompt encoder replacement is a scientific necessity. FMLM+, MLFM, and S-FLM perform inference without an external pretrained prompt encoder. To assess latent diffusion under the same inference condition, we must also remove that dependency. Retaining Qwen leaves its contextual computation inside the reasoning system, however inexpensive its forward pass may be. Inference speedups are irrelevant to this scientific requirement.

  • Benchmark advantages remain after teacher replacement. With the learned prompt encoder and DMD2-based stochastic sampling, LFRM outperforms all compared continuous-diffusion baselines at comparable backbone scales across our mathematical reasoning and coding benchmarks (Tables 2, 5, and 29).

  • The remaining accuracy gap to teacher conditioning is an important direction for future research on compact prompt encoders. Our results nevertheless demonstrate that strong reasoning performance (over comparable baselines) can be achieved without executing the external teacher at inference.

  • Reviewer responses.

    • WJDV now confirms that their main concerns are addressed, and raised their rating to weak acceptance.
    • MS2M retains concern about the accuracy drop, but raised their rating to weak acceptance.
    • g8h4 continues to characterize prompt encoder replacement as incurring “a substantial MBPP accuracy loss for modest latency savings,” despite our explanation that removing the external prompt encoder is necessary for the scientific comparison, regardless of latency savings. g8h4 has not yet responded to our follow-up explanation.

Common issue 2: Attributing NFT gains and establishing the role of gold endpoints. (WJDV, g8h4)

  • We completed the requested ablations. These comprise the four-way gold-endpoint × guidance-correction comparison and two supervised-continuation controls at matched updates and equal or greater compute (Table 4; Appendix J).

  • Guidance correction improves NFT performance beyond supervised continuation. Correction improves accuracy with and without gold endpoints; even without gold endpoints, corrected NFT outperforms both supervised-continuation controls on GSM8K.

  • Gold endpoints serve as a stabilizing regularizer. Their intended role is to guard against training degradation, and our ablations demonstrate this through substantially reduced deterioration when correction is absent.

  • Reviewer responses.

    • WJDV requested these controls and now confirms that their main concerns are addressed.
    • g8h4 states that “the independent benefit of gold endpoints remains uncertain.” We explained that ablations clearly demonstrate the gold endpoints' intended regularization effect. We requested clarification about why this evidence leaves their benefit uncertain. g8h4 has not responded with a clarification.

Common issue 3: Isolating the representation contribution. (WJDV, g8h4)

  • We completed both requested controls. WJDV requested comparisons with identical prompt representations while changing the answer representation. g8h4 requested a learned single-layer reference. We added both, matching training data, teacher resources, backbone, latent width, and training budget.
  • Multilayer representations outperform single-layer representations, for both learned and PCA projectors.
  • Learning the multilayer projector improves over using PCA.
  • Both findings hold with and without fixed prompt representations.
  • Reviewer responses. WJDV confirms that their concerns are addressed. g8h4 appears satisfied on this point: “They address most of my questions.”
AuthorsOpenReview ↗

Global Response (3/3)

Common issue 4: Matched baselines and evaluations. (5A9S, MS2M)

  • Our comparisons account for model scale, inference cost, scoring, and prompt encoding. We compare methods at comparable backbone scales and denoising budgets, measure end-to-end latency on common hardware, match coding tests and scoring rules, and separately compare models using the external teacher prompt encoder or a compact learned prompt encoder where relevant. LFRM achieves stronger accuracy at fewer or comparable denoising NFEs. Separately, our common-hardware measurements at comparable NFE show lower or similar end-to-end inference latency (Appendices M–N).

  • We completed additional baseline evaluations where possible. We evaluated available released checkpoints to fill missing comparisons, tested common prompts, and documented cases where checkpoints or inference code were unavailable. Controlled comparisons were already present in the original submission; these experiments further strengthen them.

  • Reviewer responses.

    • MS2M did not raise further concerns about missing evaluations or baseline comparability in their follow-up.
    • We asked 5A9S to identify which specific comparisons, in the original submission or added during rebuttal, they consider unfair and which uncontrolled factors undermine them. They have not responded.

5. Additional evidence and manuscript improvements.

  • Clearer motivation and experimental reporting. We revised the introduction and experimental explanations, clarified evaluation protocols, and explained missing table entries.
  • The learned-multilayer representation recipe also works with a smaller Qwen teacher. We completed MS2M's requested teacher comparison using Qwen-0.6B and Qwen-4B under matched backbone-training conditions (Appendix L.1).
  • The learned prompt encoder retains most GSM8K accuracy at equal training duration. The epoch-18 comparison holds backbone-training duration fixed while comparing the external teacher prompt encoder with the learned prompt encoder (Appendix L.2).
  • Resource accounting covers preparation, training, and inference. We documented costs across training stages and representation preparation, alongside end-to-end latency and prompt-encoder memory measurements (Appendix N).
  • Asynchronous inference improves accuracy at essentially unchanged cost. We added four-seed schedule comparisons and direct timing measurements; asynchronous gains are more pronounced with DMD2 sampling, with essentially unchanged per-NFE cost (Appendices K and N).
  • One model can serve both GSM8K and MATH500. The MATH-trained model transfers to GSM8K, and short mixed-task adaptation improves GSM8K while retaining MATH accuracy with DMD2. Broader cross-domain generalization remains future work (Appendix L.3).

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