- Rating
- 2(+1)
- Confidence
- 4
- Informativeness
- 1
- Presentation
- 1
- Soundness
- 2
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Paper summary
The paper motivates the problem statement by empirically showing that candidate tokens proposed at the same point can lead to different numbers of later accepted tokens. It derives the expected accepted length under standard lossless speculative sampling and shows that an ideal drafter would have each candidate token receive a training credit according to both the probability of reaching that point and the expected number of later acceptances after that candidate. It gives a practical implementation of this formulation via D-VOLT, which approximates this using the top four candidates and adds the resulting candidate specific reward to a distribution matching loss. The exact derivation is mathematically consistent for autoregressive speculative sampling. However, the implemented loss has a DSpark specific approximation. The reported gains support the method for one Qwen3-8B target and one DSpark drafter, but the absence of additional drafter architectures, independent training runs, uncertainty estimates, complete data splits, and broader domain evaluation leaves its generalizability unresolved.
Critical strengths
a) The problem statement has a clear motivation b) The proposed solution seems to tackle the problem statement head-on and is practical to implement.
Critical weaknesses
- The general exposition and presentation are abysmal and fall well below the standards required for a technical paper. The manuscript replaces a straightforward idea with unnecessary made up jargon/terminology by the authors and then fails to use that terminology consistently. For example, the same underlying notion is called a
continuation value,candidate value,andtoken conditional continuation value,while its use in training is variously described ascandidate specific credit,continuation credit,acandidate specific continuation reward,andvalue corrected distribution matching.
These are just two specific examples; the manuscript is full of such inconsistent unnecessary phraseology, forcing the reader to reconstruct ordinary probability and dynamic programming concepts from unnecessary jargon. The mathematical notation compounds this exposition problem with lowercase and uppercase versions of the same quantity being used inconsistently. Similarly, the paper does not clearly separate the exact full tree derivation from the substantially different training objective used in practice until a brief qualification near the end of Section 4.2. The current writing leaves a lot to be desired because it obscures which claims are proved, which quantities are approximated, and which objective is optimized. The manuscript requires a comprehensive rewrite using standardized terminologies and notation and their consistent use throughout the paper.
- The manuscript use a single drafter Qwen-8B model and single dataset ( full Open-PerfectBlend mixture). This is a pretty limited evaluation. Moreover, the actual objective is limited to the original DSpark objective and D-PACE, although the paper cites other training objectives that directly target speculative acceptance. In particular, AngelSpec optimizes cumulative products of target/draft overlap across draft positions, making it a close sequence-level alternative to D-VOLT’s accepted-length objective. LK Losses directly optimizes target/draft overlap with substantially lower reported training overhead. A controlled comparison under the same DSpark architecture, initialization, training data, and optimization budget is needed to establish whether candidate-specific continuation credit improves over these simpler acceptance-oriented objectives.
Questions for authors
a) The hyperparameter-selection described in the paper does not match the claimed evaluation scope. D-VOLT is trained on the broad Open-PerfectBlend mixture, but both the continuation coefficient and candidate count are selected using only a held-out GSM8K set. These hyperparameters will be susceptible to the validation dataset chosen, particularly because the top-K approximation may cover different amounts of target probability in mathematics, code, and open-ended dialogue. Although the selected setting has the largest reported point estimate on the four test benchmarks, the paper provides no uncertainty estimates and evaluates neither code nor chat. The authors should justify GSM8K as the sole validation domain or select the global configuration using a fixed multi-domain validation mixture.
b) The relationship between the theoretical objective and the implemented training loss requires clarification. The exact analysis derives the gradient of expected accepted length over the complete prefix tree, using exact reach probabilities and token-specific continuation values. The practical objective in Equation 7 instead uses sampled histories, top-K continuation estimates, shared histories across candidate branches, fixed exponential position weights, and a tuned continuation coefficient. The authors acknowledge that this is a surrogate, but provide no bound or empirical gradient-alignment analysis connecting it to the exact objective. Moreover, Equation 7 uses L1 distribution matching, whereas standard fine-tuning uses cross-entropy and the original DSpark objective combines cross-entropy, total variation, and confidence prediction. The paper should clarify the complete loss used for every baseline and compare L1, cross-entropy or KL, and an adaptive LK objective under the same candidate-specific continuation term.
c) Most of the presented results are for a single combination of Qwen3-8B target, DSpark drafter, and one block length. Is there any thing specific in your formuation that limits the evaluation to only Dspark drafter? The reported benchmarks are also concentrated on reasoning and multiple-choice tasks. No code or open-ended dialogue benchmark is included, even though code and chat constitute a substantial portion of Open-PerfectBlend. Because the candidate-specific continuation reward is estimated from sampled training histories, its benefit may depend on the input distribution. I am not sure how much of this new method's improvement would be transfer to cross domain distributions. Evaluation on code, dialogue, and a second target or drafter configuration would be needed to establish the claimed generality.
d) The main results report only point estimates, with no standard deviations for independent seeds, making the stability of the claimed 2 to 3 percent improvements impossible to assess. The paper also omits essential details of the training, validation, and test splits, so the principal empirical claims cannot be independently reproduced or verified.
e) As a reader, I would be more interested in understanding the failure patterns and tradeoffs introduced by D-VOLT, rather than seeing only improvements in mean accepted length. The paper does not report which inputs or token positions perform worse, whether the probability of accepting no draft tokens increases, or whether favoring candidates with longer predicted continuations reduces target matching elsewhere. Reporting these cases, together with performance under changes in input domain, would clarify when the method helps and when its training objective becomes harmful.
11 comments
Rebuttal doesn't address the concerns raised
Thank you for the additional experiments. They partially address evaluation breadth, but several responses misquote my review or leave the requested evidence unanswered.
First, I did not write that “The formulation is DSpark-specific.” I wrote that the exact derivation is general, while the implemented loss contains a DSpark-specific approximation, and asked for evaluation with another drafter architecture. The response itself acknowledges that Equation 6 exploits DSpark’s parallel logits and Markov head. All new experiments still use DSpark. Changing the target model and block length does not test another drafter architecture.
The response similarly changes my concern that GSM8K-only hyperparameter selection “will be susceptible to the validation dataset chosen” into the categorical claim that it “will not generalize.” I did not make that claim. Showing gains on other benchmarks is useful, but it does not test whether another validation domain would select different values of β and K. Likewise, I asked how much the benefit transfers across input distributions. I did not predict that transfer would fail. Code and chat evaluations broaden the evidence, but Open-PerfectBlend already contains code and chat data, so these results do not establish transfer outside the training distribution.
My requested loss comparison is entirely unanswered. I asked the authors to specify the complete loss used for every baseline and compare L1, cross-entropy or KL, and an adaptive LK objective while holding the candidate-specific continuation term fixed. The Candidate Value versus Shared Value ablation changes the continuation credit while retaining the same base loss, so it answers a different question. Mentioning alternative losses in related work is not the requested controlled comparison.
The independent-seed uncertainty concern is also unanswered. Monte Carlo standard errors and bootstrap intervals for continuation-value estimation do not measure variation across independently trained models. The response provides no number of training runs, standard deviation across checkpoints, confidence interval for the main comparisons, or evaluation-seed accounting. Reviewer 9hpN independently asked how many training runs were conducted and requested variability across seeds. The authors answered that reviewer’s Questions 1, 3, and 4 while skipping Question 2 about independent training runs. Reporting improvements in 32 benchmark settings does not replace repeated training runs.
The response also says it provides “exactly” the requested gradient-alignment analysis, but it measures continuation-value error and candidate-ranking agreement. Elsewhere, the authors admit that they “have not measured end-to-end gradient cosine similarity during training.” Value-estimation accuracy is relevant, but it is not gradient alignment. The reported 80 to 83 percent ranking agreement also means disagreement in approximately 17 to 20 percent of evaluated records.
The claimed new experiments are not in the supplied manuscript. It still contains only Qwen3-8B, a DSpark drafter with block length 7, and the original four benchmarks. It contains none of the new Qwen3.5, block-length-16, code, chat, or graph-versus-Monte-Carlo results. The authors repeatedly refer to “General Response G1” for the full per-benchmark table, but that table is absent from the current OpenReview draft. Only aggregate means and ranges are visible. I also find no supporting code, checkpoints, or raw results.
Finally, the response does not address the requested failure analysis, complete data splits, or conditions under which D-VOLT performs worse. It continues to report mean accepted length without independent-seed uncertainty or the distribution of per-request outcomes.z
The new experiments provide useful preliminary evidence across another target, additional block lengths, and broader task categories. They do not resolve the controlled-loss, independent-seed, different-drafter, reproducibility, failure-analysis, or artifact concerns. Several responses instead rebut stronger claims that I did not make. My rating therefore remains unchanged.
Problem with AI slop
My concern is not AI assistance itself. The concern is that the resulting prose changes genuine qualified questions into categorical claims, obscures unresolved distinctions, and makes the scientific response less precise. Instead of acknowledging this problem and striving to fix this in the revised draft, the authors are pretty defensive and doubling down
The authors dismiss the writing concerns raised by me in the review by separating “continuation value,” “candidate credit,” and “continuation reward” as distinct mathematical objects. That response addresses only a narrow subset of the problem. The submitted manuscript repeatedly renames the same continuation quantity as “continuation value,” “candidate value,” and “token-conditional continuation value,” then surrounds it with opaque labels such as “allocation headroom,” “granularity of continuation credit,” and “value-corrected distribution matching.” A first time cold reader cannot make sense of these non-standard jargon. None of these labels makes the underlying operations clearer. “Allocation headroom” means the maximum improvement in an estimated return under fixed probability constraints, while “value-corrected distribution matching” means L1 matching with an additional continuation reward. Stating those operations directly would be shorter and more precise.
This is not merely a stylistic preference. The manuscript’s compressed, AI-style phrasing obscures which quantity is estimated, which objective is optimized, and which parts of the exact derivation survive in the practical algorithm. The clearest example is the statement that the timing results compare “complete training configurations with different software versions and supervision paths.” The authors explicitly acknowledge in another response that an LLM introduced this “overly defensive statement,” yet it remains in the submitted manuscript and still does not identify what differed or how the differences affect the comparison. Their promise to add a glossary does not address the larger problem: ordinary mathematical operations are repeatedly hidden behind unnecessary labels, while consequential differences between the exact gradient and the implemented approximation receive only brief and indirect explanation.
The rebuttal itself continues the manuscript’s writing problem. Phrases such as “removed this concern entirely,” “directly contradicted,” “we now provide exactly this,” “the data shows no such effect,” “consistent, low-noise signal,” and “surrogate fidelity” are vague or inflated substitutes for stating what was actually measured. Several of these claims overstate the evidence: value-ranking agreement is presented as gradient alignment, transfer across task categories is presented as robustness to distribution shift, and a second target model is presented as resolving the absence of another drafter architecture. The authors also acknowledge in another response that they used an LLM to summarize experimental results and that it introduced “an overly defensive statement.” The same defensive, formulaic style remains throughout this rebuttal.
We respectfully disagree with the reviewer's overall assessment. Several of the central criticisms rest on factual misreadings of the paper, which we correct below. Where a concern is empirical, we answer with new experiments.
1. "Single dataset." This is incorrect. Open-PerfectBlend is the training mixture. The paper evaluates on four separate benchmarks (BBH, MMLU-Pro, WinoGrande, and GSM8K) at two decoding temperatures. Treating the training corpus as the evaluation scope conflates two different things.
2. "Single target / single drafter / single block length; no code or dialogue." We have now removed this concern entirely (General Response G1). We trained matched DSpark and D-VOLT drafters for Qwen3-8B with B=16 and for a different, larger MoE target, Qwen3.5-35B-A3B with B=8. Each was evaluated at T=0 and T=1 on eight benchmarks spanning reasoning, code (MBPP, HumanEval), and open-ended chat (IFEval, Arena-Hard-Auto). D-VOLT improves accepted length in all 32 of 32 settings. Gains are +3.8% to +5.4% on code and +6.0% to +8.1% on chat. The reviewer's hypothesis that the benefit "may not transfer to cross-domain distributions" is directly contradicted. Code gains are on par with reasoning gains (mean +4.7% vs. +5.2%), and chat gains are the largest of any domain (mean +7.0%).
3. "Hyperparameters selected on GSM8K only will not generalize." The new results test this directly. With the same defaults, the gain on GSM8K itself (+4.0% to +4.9%) is at or below the median in every one of the four new settings, while chat gains exceed it in all of them. If the configuration were overfit to the selection domain, we would expect the opposite pattern. The data shows no such effect.
4. "The formulation is DSpark-specific." This is incorrect. The Bellman recursion and the exact gradient decomposition (Eqs. 4–5) are stated for any autoregressive drafter under standard lossless verification. They use no DSpark structure. Only the efficient estimator in Eq. 6 exploits DSpark's parallel base logits plus Markov head. For a sequential drafter, the same DP runs over a top-K tree built from the drafter's own proposals. The new B=8 and B=16 results confirm that the method is not tied to one block length either.
5. "No empirical gradient-alignment analysis connecting the surrogate to the exact objective." We now provide exactly this (General Response G2). Using the same checkpoint and prompts as Appendix A, we compared the practical estimate (Eq. 6) against an unbiased full-history Monte Carlo estimate of the exact value (Eq. 4). The study covers about 18.5k (block, position) records per setting at K∈{4, 8, 16}, with bootstrap CIs and an explicit MC noise ceiling.
The surrogate therefore tracks the ordering that drives the exact gradient, and its residual bias is quantified rather than unknown. We also note that the paper never claims Eq. 7 is the exact gradient. Sec. 4.2 explicitly calls it a practical surrogate and lists each approximation, which contradicts the claim that the paper "does not clearly separate" the two.
6. "Made-up jargon used inconsistently." The terms the reviewer lists as synonyms denote three different mathematical objects:
"Token-conditional" is not decoration. It marks the paper's core contrast with prior objectives that use a continuation weight shared across candidates. Bellman recursion, reachability, and backward DP are standard terms, used in their standard sense. That said, we will add a one-line glossary and use a single name for each object.
7. Effect size. The review refers to "the claimed 2 to 3 percent improvements." That range corresponds to the Candidate- vs. Shared-value ablation (1.76%–3.04%), which is a deliberately strict control. The headline gains over DSpark are 4.05%–9.74% (Table 1). The new experiments add 32 further settings, with gains of +1.4% to +9.1% and a median of +5.1%.
We hope that, in light of these corrections and the new evidence on generality, cross-domain transfer, and surrogate fidelity, the reviewer will reconsider the score.