Training Free Guided Flow-Matching with Optimal Control

Thank you for the great suggestion. Following your suggestion, we now provide comprehensive discussion on time and memory complexity in appendix D, including theoretical complexities for OCFlow, baselines and RedDiff (table 6) and actual runtime and memory usage of OC-Flow/Dflow/FlowGrad (table 8-10). You’re absolutely correct that the family of methods that optimizes ODE trajectory (Dflow/FlowGrad/ours) share the same limitation of inducing higher computation cost compared to posterior sampling (e.g. RED-Diff, DPS). To mitigate the cost, we introduce both an asynchronized update and adjoint method with vector-jacobian-product implementation on both Euclidean and SO3 to drastically reduce memory and runtime complexity on SO3 from O(D^4) to O(D^2) (table 7), while also being more efficient than Dflow (e.g., memory cost $O(ND^2)$ -> $O(D^2)$). This effectively enables us to sample 256x256 image under 3.5min whereas Dflow (without gradient ckpt) ran OOM on image task. The self-reported runtime for Dflow on 128x128 image is 15min, significantly higher than our efficient implementation of OC-Flow. Note that this is potentially because DFlow highly relies on the use of L-BFGS optimizer to achieve reasonable results (see our ablation on optimizer table 11), which adds a lot of runtime complexity due to e.g., uncontrollable line search complexity in L-GFBS. Our implementation of OCFlow-SO3 is also efficient (at the same order as Euclidean) and only 1.5x the runtime for Euclidean (e.g., 296s for SO3 and 188s for Euclidean in peptide design).

We compare the cost of producing one sample in our method relative to direct sample without optimization, and the ratio is approximately 30x, as you predicted. We have updated discussion to talk about the tradeoff between computation cost and performance in comparison to “plain approach” like Red-Diff (line538). We believe that users could decide the tradeoff depending on applications and OC-Flow would be especially valuable for applications that require better quality and reward optimization with less latency requirement.

Q1: regarding proposition 1

We appreciate your valuable feedback regarding the ambiguity in notation. We have updated proposition1 with clearer notation definitions and extended theoretical results to bounding marginal distributions. The intuition here is to theoretically show that the running cost can control deviation from prior distribution measured by KL-divergence.

For part 1 of proposition1, for a specific deterministic path of the prior model, its terminal point is defined as $x_1^p$ and the data used to train this path is $x_1$. Through the training process, the conditional distribution of the terminal point of this path given the training point is a delta distribution. However the joint distribution of $x^p$ and the training samples $x_1$, given by
$p_{1}(x_p, x_1) = p_{1}(x^p|x_1)p_{data}(x_1)$
is not a delta distribution. As the control terms are defined per sample, it is reasonable to consider them as being incorporated into the conditional path $p(x|x_1)$ and then marginalized. This is because, as you noted, the ODE path is deterministic, and focusing on a specific path corresponds to dependence on a specific training sample $x_1$, which defines the path.

However, we acknowledge that it is probably more ideal to bound the marginal distribution, and therefore we now provide additional result in proposition 1 which establish the KL bound between marginal distributions of prior and guided model as a function of running cost, under slightly more limiting assumptions (Appendix C.1.2).

Thank you for your insightful follow-up questions, we are happy to provide our answers as follows:

Q1. Regarding DPO applied on a conditional reward function.

Thank you for the question. We’d like to note that the training time we used as reference here is from the DRaFT paper[1] which is finetuned for a fixed and relatively easy reward (Aesthetic Score, compressibility, etc.). It is probably better if we said “More than 2880*8 images are needed for a fixed reward function”. As we mentioned in the rebuttal, amortizing the reward optimization effectively relies on the model’s capability to generalize to any new reward landscape conditioned on any prompt, which is by far still a challenging issue in RLHF. DPO(or in general RLHF) is known to be subject to overfitting and model collapse[2][3], and to our knowledge, there hasn’t been a really strong theoretical guarantee of how DPO can generalize across very different domains/conditions. From the RL point of view (if we view the prompts as part of the state), optimal policy convergence is often only guaranteed with sufficient coverage of all possible states (meaning it’s less data efficient), and it is usually globally greedy (instead of per-state optimal).

Meanwhile, the actual time required for alignment with complex conditional reward functions could be much higher than 196 GPU hours. E.g., SD3[4] reported 2K iterations DPO finetuning on 8B models, effectively requiring 16T parameter updates. That said, we do not want to claim that inference-time guidance is necessarily better than RLHF. As noted in our rebuttal, we believe there are pros and cons for both, and the choice of the methodology should depend on the use cases and the scale of the problem.

Q2. Clarification on conditional probability $p_1(x|x1)$ in proposition 1

Thank you for the detailed question. We now realize where the confusion is from and have adjusted our description of Proposition 1 for better clarity. In part 1 of Proposition 1, we analyze the effect of control terms $\theta(x_1)$ when they are applied to the conditional probability path $p_t(x^p|x_1)$ given a terminal data $x_1$ which is induced by a conditional vector field and is probabilistic, instead of a single deterministic ODE trajectory simulated with a trained marginalized vector field and fixed noise $x_0$. This allows us to analyze probabilities with a more tractable form than the complex push-forward equation and get tighter bounds. Note that in a guided sampling setting, a different set of control terms are solved for each $x_1$ (or equivalently $x_0$ due to deterministic ODE), and therefore we note control terms as $\theta(x_1)$ to illustrate its dependency on $x_1$. Overall, this analysis states the effect of $x_1$-dependent control terms on Gaussian paths conditioned on target training data $x_1$, to help us get some intuitions on the potential effect of $\theta(x_1)$ before marginalization. As we mentioned in the rebuttal, we acknowledge that bounding marginal distribution induced by controlling the marginal vector field is more ideal, and therefore we added part 2 which is directly derived from applying the push-forward equation.

Another way of understanding part 1 is to imagine our controlled generation as a few-shot finetuning scenario, where the target data $x_1$ is given and fixed. Therefore, we still need to rely on conditional paths as in the training stage but can start off from a known prior generative model $p^p(x_t|x_1)$ to consider the distance to the “finetuned” model $p^\theta(x_t|x_1)$. Note that this is purely a thought experiment to provide an intuition of our OC-inspired framework, as we have demonstrated in later theorems that such expensive finetuning can be effectively replaced by our iterative OC-Flow algorithm in Alg 1.

We hope the above discussion addresses your questions, and we're happy to continue the inspiring discussion if further questions arise.

[1] Clark, Kevin, et al. "Directly fine-tuning diffusion models on differentiable rewards." arXiv preprint arXiv:2309.17400 (2023)

[2]Zhu, Banghua, Michael Jordan, and Jiantao Jiao. "Iterative Data Smoothing: Mitigating Reward Overfitting and Overoptimization in RLHF." Forty-first International Conference on Machine Learning.

[3] Xiong, Wei, et al. "Iterative preference learning from human feedback: Bridging theory and practice for rlhf under kl-constraint." Forty-first International Conference on Machine Learning. 2024.

[4]Esser, Patrick, et al. "Scaling rectified flow transformers for high-resolution image synthesis." Forty-first International Conference on Machine Learning. 2024.

We sincerely thank your insightful feedback and your high recognition of our work’s theoretical innovation from the optimal control perspective and consistent improvement over various datasets from different ML domains. We’re happy to address your questions and concerns as follows.

Q1 Scalability and Real-time applications Thank you for the perspective. We have provided a comprehensive theoretical analysis and empirical evaluation of the runtime and memory complexity of OC-Flow and other baselines in our revision (appendix D) and common rebuttal. We note that the text-image alignment task on the CelebA-HQ dataset contains images with a resolution of 256x256x3, which is potentially larger than the average size of protein backbone data (Lx3). We acknowledge that differentiate-through-ODE approaches (OC-flow, Dflow, FlowGrad) are by nature more computation-heavy than the posterior sampling approach, despite its outstanding guidance.

Performance. Nevertheless, we have particularly designed efficient algorithms on both SO3 and Euclidean, e.g., asynchronized update, adjoint method, and vector-jacobian-product implementation, which significantly reduced the time and memory complexity on SO3 from O(ND^4) to O(D^2) (see table 1 and Appendix D table 7), and also advantageous compared to DFlow on Euclidean (i.e. reduce memory cost from O(ND^2) to O(D^2), and runtime efficiency from $O(cND^2)$ to $O(nD^2)$ as we don't rely heavily on L-BFGS, as shown in Table 11). Our empirical benchmark of runtime demonstrates speedup and memory saving compared to Dflow. We show that OC-flow samples 256x256 image in 216s, and small molecules in 38s, which might be tolerable for certain real-time applications depending on latency requirement, as opposed to Dflow which self-reported to take 15min on 128x128 image and ran OOM in our image dataset. Following your suggestion, we include discussion on scalability and time complexity in the discussion section. We acknowledge that real-time application of our method may depend on multiple factors such as size of the model, data and hyperparameters during sampling such as number of control terms and iterations. Still, OC-Flow provides an advantage compared to existing approaches in the same family, and would be valuable for applications where high sample quality and reward optimization is desired.

Q2 Intuition behind Theorems We have updated the theoretical proof in our revised manuscript with clearer notation definitions, intuitive motivations (line 167), and some corrections on some inadvertent notation errors. We’d like to clarify that the KL bond in proposition 1 is not between a model and a terminal point, but between the sample distribution of the pre-trained model and the guided model. The intuition here is to theoretically show that the running cost can control deviation from prior distribution measured by KL-divergence. We found that bounding the divergence between joint distribution p(x, x_data) gives cleaner and tighter bounds. However, we note that it is probably more ideal to bound the marginal distribution, and therefore we now provide additional result in proposition 1 which establish the KL bound between marginal distributions of prior and guided model as a function of running cost, under slightly more limiting assumptions.

Proposition 1 is crucial for our OC-Flow framework, as it provides theoretical guarantees for the optimal control formulation and practical algorithms for applying such a control:

• By tuning the control term $\int_0^1 \|\theta_t\|^2 dt = 0$, we can indeed control how far away our guided model deviates from the pre-trained model to prevent adversarially hacking the reward.
• By using the control term $\int_0^1 \|\theta_t\|^2 dt = 0$, we circumvent the intractable KL divergence calculation while still enjoying the theoretical benefits from optimal control.

2. Experimental significance and reproducibility

• Following your suggestion, additional experimental details are now included into the Experiment section and Appendix E, where we have reported all implementation details necessary to reproduce the results. Additionally, the code is being prepared and will be made publicly once accepted, and we've provided an anonymous link under overall comment for you to access our code for inspection. We’d like to clarify that we do not train any new FM models and the only place training is required is the reward function in QM9. To make sure fair and reproducible comparison, all of the pretrained FM models we used are open-sourced publicly available models (unlike in Dflow). We also control the initial noise and optimization parameters to be the same across methods.

• Statistical significance of the result: our results are averaged over a large number of random samples (~10³) and therefore have high statistical power. E.g., in text-to-image experiment, 1000 images were sampled for each of the 5 text prompts, resulting in a total of 5000 samples. For QM9, 1000 samples were drawn per property and per model, and for the peptide design experiment, 1620 samples were generated (162 pockets, each sampled 10 times). Given the large sample sizes, we believe the mean statistic itself is significant enough as the standard error and confidence interval is small. Furthermore, our presentation follows the same format as in FlowGrad and DFlow papers, where CIs were not required as the sample size is very large.

• In the experiment of peptide generation, the goal is to show effective of guided FM method on optimizing MadraX energy (which is reward function used to guide FM), while staying close to pepflow’s prior distribution. Therefore, metrics like SSR/BSR/RMSD are provided to show OC-Flow samples’ characteristics are similar to PepFlow samples’ and not necessarily need to be better. Thus, we do not claim that 0.793 is better than 0.795, but rather showing that they remain similar after guidance.

We’d like to also clarify that our focus is on both Euclidean and SO3, instead of only SO3. Our results on image and QM9 are in Euclidean, and our method achieve top performance uniformly across both manifolds.

3. SO3 ablation

• Thank you for your suggestion on presenting the performance of our algorithm in $\mathrm{SO}(3)$. We now include additional ablation study in Table 5 and appendix E.3. We show that OC-Flow on SE(3), i.e. combination of Euclidean (translation) and SO3 (rotation), achieved best performance, and applying OC-Flow to single modality (SO3 or Euclidean) alone can also improve Pepflow as well. As shown in Table 5, incorporating $\mathrm{SO}(3)$ optimization doubles the increase of the Madrax score from 0.34 to 0.68 compared to only optimizing translation (Euclidean).

• Additionally with table 12, we provide ablation study to show the necessity of OC-Flow-SO3 on guiding flow matching on rotation (which is a SO3 manifold), where naively applying gradient update with projection to tangent space of SO3 fails to optimize and even lead to worse samples than unconditional generation.

4. Runtime and scalability

Thank you for the suggestion. We now provide comprehensive discussion on time and memory complexity in appendix D, including theoretical complexities for OCFlow and baselines (table 1, table 6) and actual runtime and memory usage of OC-Flow/Dflow/FlowGrad (table 8-10). A key contribution we offer is the practical and efficient implementation of OC-Flow in both Euclidean and SO3, through introduction of Vector-Jacobian-Product formulation (eq15 for SO3, 3.2.1 for EU) and asynchronized update (3.2.2), which effectively reduce complexity from O(D^4) to O(D^2). We detailed the effectiveness of these scalability efforts in table 7.

Our efficient SO3 implementation mitigates the complexity of the algorithm, which is shown to be in the same order as the Euclidean version (O(D^2)). Our runtime profile in peptide design (table 9) proves that sampling of rotation (so3) only cost 1.5x of the time that of sampling translation (eu), and does not add “significant computational cost”.

Our method samples 256x256 image under 3.5min, whereas Dflow ran OOM on the same image task. The self-reported runtime for Dflow on 128x128 image is 15min, significantly higher than our efficient implementation of OC-Flow.

We sincerely thank you for your detailed and comprehensive feedback, and we’re happy to provide further clarifications and results to address all your comments:

1. Significance of our contribution

We’d like to first elaborate on the scope and significance of our contributions to address an important potential misunderstanding.

• Our work is the first one that establishes a general and formally defined optimal control framework for guiding pre-trained flow-matching models and proposes solutions that optimize the true OC objective (eq2) that comprise both the reward term and the running cost $\int_\|\theta_t\|^2$. We provide novel, theoretically grounded, and empirically effective algorithms for both Euclidean and SO3, instead of merely an extension to SO3. We note that running cost is crucial in controlling how much the guided distribution diverges from the pre-trained CFM distribution. Prior to our work, no algorithms handled the running cost properly. Our flexible framework enables tunable tradeoffs between reward maximization and faithfulness to the prior distributionwhich previous methods cannot offer as they ignore running costs and only focus on naively back-propagating reward gradients with ad-hoc-ly chosen fixed parameters.Solving the OC problem is nontrivial, as it involves optimizing objectives containing integrals and complex dynamics that naive SGD cannot address. Making sure the algorithm converges is essential to guarantee the best tradeoff between reward optimization and closeness to prior, and a non-converging naive SGD solution could lead to complete failure (e.g., table 12). Although we show that Dflow and FlowGrad are one special case of OC-Flow in Euclidean space, the OC perspectives were not offered in their original papers, as they primarily focus on naive reward gradient backpropagation. We believe the perspectives and technical depth of OC-Flow exceed far beyond the scope of Dflow and FlowGrad, therefore categorizing it as an “extension” or “generalization” is improper.

• Our focus and scope cover both Euclidean and SO3, instead of only SO3. Our results on image and QM9 are purely in Euclidean data, and our method achieves top performance uniformly across both manifolds, unlocking a wide range of real-world applications.

• We respectfully disagree that our contribution on SO3 is trivial. Firstly, we now provide comprehensive ablation study to demonstrate the contribution of OC-Flow-SO3 in peptide design. We also show how naive solutions of applying SGD on SO3 by projection to tangent space will fail (see table 5 and 11). Secondly, solving dynamics on SO3 is significantly harder than on Euclidean, and we provide not only novel convergence bounds on SO3 but also efficient algorithms that significantly speed up the computation (see general response and runtime discussion below) with VJP (section 4.3 and C4). We believe our result not only enables guiding rotation generation in protein but can also be significant to OC community and may benefit robotics/control as well.

• Finally, we clarify that OC-Flow’s focus is not on training CFM or proposing new FM models, but rather on guiding the sampling process of FM with OC to achieve conditional/constrained generation, which we state clearly in title/abstract. Our method is an inference time procedure that deviates significantly from normal forward ODE sampling and not a “trivial extension” of FM. We reviewed suggested Fjelde’s work, and it talks about the general CFM formulation and training, which is orthogonal to the problem we’re studying. We also cannot find any formula in Fjelde et al., that is close to eq2 in our optimal control framework.

• Regarding the question “I would like to see a clearer presentation of a conventional FM,..., ideally in the form of before/after equations to get an idea of the elements being added/proposed.”:
  We now improved our figure 1 and its caption to better demonstrate the OC-Flow procedure. In the high-level, the state flow at iter=0 is the original ODE trajectory of prior model (the typical CFM inference), through iterative update of costate and state trajectory we achieve the final guided sample. Another way of telling the difference for before/after is by contrasting eq1 (prior model’s dynamic), with eq2 (OC dynamic, more defined in eq4/eq8), where vector is altered by control term $\theta$ and follows $\dot{x}_t^\theta = h_t(x_t^\theta, \theta_t)$ and a complex optimization loss on trajectory terminal reward and running cost is applied, that requires iteratively update control and trajectory to solve optimal control.

Dear reviewer jxTp, once again we sincerely appreciate your detailed and constructive feedback. Following your suggestions, we have improved our manuscript and we believe our rebuttal addressed all of your comments which we summarize as the following:

Following your kind suggestion, we addressed your comments on OC-Flow’s significance, discretization errors, and its significance and scalability in SO(3) tasks. A theoretical bound for discretization error is included in Appendix C.3, along with additional theoretical analyses and empirical studies on the running memory and time also provided in Appendix D and Table 6, demonstrating the better scalability of OC-Flow. The significance of OCFlow-SO(3) is supported by extensive ablation results in Table 5 and 12, and its scalability is detailed in Table 7 and 9. We also improved our presentation by providing more interpretations and motivations of our algorithm and clearer notation definitions and figures. We include extensive experimental details in Appendix E, and we have also provided links to our codebase to enhance reproducibility. We provided detailed explanations of our contributions, key notations (e.g., costate), and paper organization to address your questions.

We really appreciate your valuable suggestions. We hope that our rebuttal has addressed all your concerns and questions, and we'd appreciate it if you could kindly respond if there are any further questions.

I would like to thank the authors for taking the time to address some of the comments/concerns. In particular, I note the addition of significant details pertaining to the experimental setup as well as some additional analysis of the discretization error in the appendices.

While some of the writing could still benefit from a bit more polish (and I note a lack of confidence intervals for many of the reported results), the authors did close some of the gaps I had mentioned. I revised my score.

Thank you for recognizing our theoretical significance, motivation and clear presentation. We fully understand your concerns, and we’d like to assure you that reproducibility has been our top priority. In fact, we spent a lot of effort in making sure our benchmarks are valid, fair, and reproducible, instead of unquestioningly copying numbers from papers, which we detail as below:

1. FlowGrad is reproducible We note that FlowGrad authors have kindly open-sourced all necessary files (code, checkpoint, scripts) and disclosed adequate details for us to exactly reproduce their experiments. Therefore, it helps us save a lot of effort and ensure fair comparison with their reported results directly.

2. Discrepancy with D-Flow self-reported result On the contrary, during our reproduction of the D-Flow baselines for molecule generation on the QM9 dataset, we noticed a critical lack of model checkpoints, code, and reproduction instructions, which prohibited direct comparison to their numbers. In guided generation task, both the base pretrained flow model (used as prior) and the reward model will impact the generation result, therefore we believe a fair comparison should be done using same generative prior model and reward model. However, DFlow paper trained their own prior model and reward model, and as of today still have not open sourced both models. We have tried contacting the authors but ended up hearing no response. Without the reward model, we cannot guide and evaluate our samples to match their setting. Therefore, we strongly argue that direct comparison with their table 4 is both unfair and unreasonable, due to unwilling discrepancies in both generative priors and reward models. In our effort to improve reproducibility, in our reproduction of the D-Flow baseline, we instead used the publicly available checkpoint from the EquiFM model, a flow-based molecule generative model trained on QM9. Though the base model architecture may not be as good as the newer one trained in the D-Flow paper, we believe such an approach ensures the reproducibility and rigor of our experiment, and benefit future benchmarking effort as everyone now has access to the model weights and can fairly compare. In our QM9 benchmark, all the methods use the same prior model (EquiFM) and same reward model we trained, and we also control the initial noises to further reduce variance.

Our training of the reward model (molecule property predictor) closely resembles Dflow’s implementation, which is detailed in our appendix E.2. Our predictions (table 3) match the ones reported in Dflow, although there is inevitable variances between two NN models even if they are trained on same data.

Our reproduction of Dflow strictly followed the hyperparameter choice in their paper and used the LBFGS optimizer with 5 inner steps and 5 outer steps (lbfgs is very important for Dflow to perform well according to our ablation table 11). Our experiments of the D-Flow baseline demonstrated a similar trend to the original D-Flow paper results, and the consistent but minor performance gap in all properties indicates this is a systematic behavior that should be attributed to the difference in the pre-trained generative model.

Tested with the same publicly available pre-trained generative model, we believe our benchmark results are more comparable and reproducible. We will open-source our code and reward model for reproducibility once the paper gets accepted.

Dear reviewer faUf,

Thank you for engaging in discussions with the authors.

I'd like to stress that sharing an anonymized version of the code is not a mandatory requirement for acceptance at ICLR. Therefore, the initial absence of shared code by the authors should not be used as a reason to recommend rejection. The only relevant guidelines that I am aware of are the author guidelines on reproducibility statements. These guidelines state that a reproducibility statement is strongly encouraged, but optional, and can potentially include an anonymized link to code. Therefore, in your review, focus on judging reproducibility aspects as much as possible based on the content and information provided in the paper and the rebuttal, and where appropriate see if the shared code can help alleviate any specific concerns that you have based on the paper. If you have any remaining reproducibility concerns or concerns of other sorts after the rebuttal of the authors, please clarify clearly why this is the case so that your recommendation can be constructive to the final paper recommendation.

Finally, please treat the code that the authors have kindly made available as strictly confidential.

Many thanks,

AC

Dear AC, thank you for your kind effort in facilitating a constructive conversation and overseeing the review process for fairness and adherence to ICLR’s reviewer and author guidelines, especially for mentioning the reproducibility policy, and the focus on making judgments based on the content and information provided in the paper and the rebuttal.

Dear reviewer faUf, we value constructive feedback and respect the rigor of the review process, and would like to continue the discussion on experimental differences to further address several key points:

Regarding your claim that we “reported vastly different metrics”

We respectfully disagree with the characterization that we reported “vastly different metrics.” For the unconditional generation with PepFlow, our implementation was validated by the PepFlow authors, and our statistics such as RMSD, SSR, and BSR align with published numbers and are even better on RMSD/BSR. Regarding Dflow, despite the significant challenges posed by the lack of access to their self-trained FM model, reward model, and Dflow implementation, we strived to produce results that remain comparable, with deviations ranging from 3% to 12%. We believe such deviation does not constitute "vastly different", especially when a different prior FM model and reward is used. We believe rerunning baselines when using new scoring functions (i.e. reward model) and experiment setting (i.e., base model) is a very common and reasonable practice, which many papers adopted without the need to excessively explain the discrepancy caused by such rerun, not mentioning that the discrepancy if caused by close-sourced nature of the baseline which we do not have control of.

We also want to mention that the phenomenon where Dflow’s performance varies with the change of the base model can be theoretically explained and understood well. As we mentioned in the introduction, a potential limitation of Dflow is the “strong confinement to the prior” which “might hinder optimization when the target reward function diverges from the prior distribution”. Specifically, Dflow strictly projects gradients onto the model-induced manifold and only moves the noise, which may not be sufficient or optimal. OC-Flow instead uses multiple control terms that allow the trajectory to deviate from prior ODE for better reward optimization while controlling the divergence from a prior distribution with effective running cost. We believe the fact that Dflow performance deviated when switching from an author-trained FM model to an open-sourced EquiFM model is exact evidence of DFlow’s strong adherence to the base model, which aligns with our observation that there might be too few controls in Dflow to guard against imperfections in prior. OC-Flow instead offers tunable tradeoffs between reward maximization and faithfulness to the prior distribution, with a good theoretical convergence guarantee.

Consider the seminal "Attention is All You Need" paper, a landmark in our field with over 140,000 citations. Its reproducibility has also been questioned, where BLEU scores relative differences often exceeded 20%. As highlighted in the widely cited paper, "A Call for Clarity in Reporting BLEU Scores" (2,800 citations), reproducibility challenges are not uncommon for impactful works. We believe focusing disproportionately on unwilling and unavoidable reproducibility differences—especially for baselines without released code or models—risks detracting from the broader contributions of new research.

Finally, we’d like to reiterate why the proposed comparison is unreasonable: in a guided generation task, request to reproduce the “MAE on QM9 author-trained reward model prediction of Dflow-guided, author-trained flow model samples” and comparing with such result when none of the necessary resources—the reward model, the author-trained flow model, or the Dflow implementation—are publicly available is unfair and unreasonable. To illustrate, this is analogous to comparing the results of “guiding SD3 with CLIP reward and method A” against “guiding SD1.5 with AlphaCLIP reward and method B”, which is unfair and scientifically unmeaningful. We also respectfully disagree with the assertion that Dflow’s peer-reviewed status warrants blind acceptance and use of its reported results. Furthermore, there is no evidence that Dflow has undergone the same level of scrutinization as reviewer faUf requested, and even as of today, there is no publicly available codebase from Dflow that allows academic researchers to objectively examine its claim.