acceptodds
Under review as a conference paper at ICLR 2027

Learning Where to Go: Spectrally Aligned Surrogates and Search for Offline Model-Based Optimization

Abstract

In offline model-based optimization (MBO), the quality of a learned surrogate is determined not only by how well it captures preferences among observed designs, but also by whether its geometry provides reliable directions for optimization beyond the training distribution. Standard learning objectives can preserve useful predictive structure while still admitting high-frequency variations that produce unstable or misleading gradients during out-of-distribution search. We introduce SASS (Spectrally Aligned Surrogates and Search), a framework that aligns surrogate learning and search through a shared spectral inductive bias. SASS trains the surrogate to preserve its induced preferences under high-frequency perturbations, encouraging reliance on stable low-frequency structure while suppressing variations that distort the optimization landscape. At search time, gradient updates are projected onto the same low-frequency subspace, so that surrogate learning and optimization are governed by a common notion of stable structure. Across five Design-Bench tasks, SASS improves over both ranking baselines in mean normalized score on every task. Further analyses assess how spectral projection preserves objective values and rankings, and identify conditions under which the low-frequency assumption breaks down.

Primary area:
optimization
Keywords:
offline model-based optimization

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_8CDgOpenReview ↗
Rating
3
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper introduces SASS, which unifies the spectral-ranking consistency regularization used during surrogate model training with the gradient projection employed during the search phase by sharing a low-frequency Fourier projection, PρP_\rho. The authors evaluate SASS against various offline MBO baselines across five tasks from the Design-Bench benchmark. Furthermore, the paper provides a conditional trajectory analysis to characterize the deviation of the projection-based search from standard gradient ascent.

Critical strengths
  1. This paper's problem positioning is novel: instead of pursuing higher ranking accuracy, it clearly distinguishes between the two distinct objectives of "ranking quality" and "search direction reliability," which is insightful for offline MBO research.
  2. SASS aligns learning preferences with search constraints through a single spectral projection, making its design more unified than mere surrogate regularization or simple search improvement.
Critical weaknesses
  1. The theoretical results are relatively weak and fail to provide guarantees for end-to-end optimization. The analysis of trajectory conditions in Section 3.3 relies on the assumption that ∥Qρ∇sθ(x)∥≤ϵ\|Q_\rho \nabla s_\theta(x)\| \le \epsilon, along with a Lipschitz condition on the gradient. However, the authors explicitly acknowledge that these assumptions are neither automatically satisfied by the consistency loss nor applicable to the ReLU surrogate networks used in practice. More importantly, this analysis merely indicates that the divergence between the trajectories of projected search and standard search is bounded by ϵ\epsilon. It neither proves that the true objective function will increase nor offers any guarantees regarding the quality of the candidates. Consequently, this theoretical result serves more as a conditional explanation than as a robust validation of the method's effectiveness.
  2. The paper argues that accurate ranking alone is insufficient for reliable offline MBO, but the role of ranking deserves a more nuanced discussion. I encourage the authors to cite and discuss On the Learnability of Offline Model-Based Optimization: A Ranking Perspective (Lyu et al., 2026, arXiv:2603.04000), which theoretically characterizes the importance of optimization-relevant ranking errors. Clarifying the complementary roles of ranking accuracy in candidate selection and surrogate gradient geometry in guiding search would strengthen the paper's motivation and theoretical positioning.
  3. Evidence for frequency robustness has not yet been localized to specific components. The perturbation robustness experiments in Section 4.4 evaluate the complete SASS framework only on the Superconductor dataset. The authors explicitly note that these comparisons "do not isolate which component accounts for the difference."
  4. Section 4.5 evaluates the preservation of oracle quality before and after projection using the Spearman correlation coefficient and RMSE. However, such metrics only assess whether the projection retains the target correlation values or rankings; they do not directly measure the magnitude of Qρ∇sθ(x)Q_\rho \nabla s_\theta(x), nor do they evaluate the degree of alignment between the projected gradient and the true local direction of the target.

Some typoes:

  1. In Section 2, the symbol V∈{Y,Z}V \in \{Y, Z\} is used in a way that conflates vectors with indices; it is recommended to change this to R∈{Y,Z}R \in \{Y, Z\} or to explicitly use V(Y)V^{(Y)} and V(Z)V^{(Z)}.
Questions for authors
  1. Please supplement the ablation study on the robustness of individual variants C1, C2, and C3 under high-frequency perturbations, and repeat the key robustness experiments on at least one other task (such as TF-Bind-8 or TF-Bind-10) to determine whether the robustness is consistent across tasks.
  2. Please report the empirical distribution of Qρ∇sθ(x)Q_\rho \nabla s_\theta(x), or compare the correlation between the projected gradient and the oracle finite difference direction to directly test the core mechanism that "high-frequency gradient components lead to unreliable search".
  3. Clarifying the complementary roles of ranking accuracy in candidate selection and surrogate gradient geometry in guiding search.
3 comments
AuthorsOpenReview ↗

Response to Reviewer 8CDg [1/2]

We appreciate the reviewer’s attention to the distinction between ranking quality and search-direction reliability. Below we clarify what the theory establishes, identify the component-level analysis in the appendix, and present new robustness and gradient-alignment results.

1. Scope of the theoretical analysis

The trajectory bound does not guarantee oracle improvement or end-to-end convergence. Section 3.3 and Appendix C.4 state its assumptions separately from the consistency loss; in particular, they do not follow automatically for the ReLU implementation.

The analysis has two roles:

  • Constrained update interpretation (Eq. 13): The projected step exactly maximizes a regularized first-order surrogate objective within the retained subspace.
  • Conditional trajectory characterization (Eqs. 14–16): Under the stated smoothness and complementary-gradient assumptions,

∥ut−vt∥≤ϵL[(1+ηL)t−1].\lVert u_t-v_t\rVert\leq\frac{\epsilon}{L}[(1+\eta L)^t-1].

The bound relates the magnitude of the removed gradient to finite-horizon trajectory discrepancy. It says nothing about which trajectory achieves a better true objective value. We will clarify this distinction and reserve claims about optimization performance for the experiments.

2. Complementary roles of ranking and gradient geometry

Ranking helps identify and select promising designs, while surrogate gradients determine the local directions used to generate new candidates. Agreement on observed rankings alone does not determine these directions outside the observed designs.

Appendix Figures 3–4 illustrate this distinction: synthetic surrogates with nearly matched ranking metrics exhibit different gradient errors, trajectories, and final oracle values. Table 5 addresses a separate question—preservation of oracle rankings under input projection—and is not a direct measure of learned ranking accuracy or gradient reliability.

Thank you for suggesting Lyu et al. (2026). Their analysis relates optimization-relevant ranking to design quality, while Section 6 explicitly identifies path-dependent optimization and local gradient behavior as a remaining issue. SASS empirically investigates this aspect by applying a shared spectral constraint to surrogate learning and search. Our focus on gradient-based candidate generation therefore complements their ranking perspective. We will clarify this connection in the revision.

3. Component-level robustness and an additional benchmark

Appendix Table 10 reports the individual-component analysis on Superconductor. Under high-frequency-directed training-input corruption at severity 0.20, the drops for Base, C1, C2, C3, and Full SASS are 0.047, 0.028, 0.027, 0.046, and 0.018. Section 4.4 discusses full-framework comparisons; we will add a clearer pointer there to this component-level analysis.

We also repeated the component-level evaluation on TF-Bind-10 to test whether the pattern holds on another task. High-frequency-directed perturbations were applied to continuous logits, rescaled to severity 0.20, using five matched seeds and identical corruption protocols across variants.

Table R1. Component-level robustness on TF-Bind-10 (mean ± SD).

VariantScore drop ↓
Base0.054 ± 0.009
C10.037 ± 0.007
C20.035 ± 0.007
C30.052 ± 0.009
Full SASS0.022 ± 0.005

Results are reported as mean ± standard deviation across five matched seeds, computed from seed-level clean-to-corrupted paired score drops.

Both tasks show the same pattern: C3 alone is close to Base, C1 and C2 reduce the drop, and Full SASS performs best. This points to a role for the training-time components in the tested corruption settings, without extending the claim to arbitrary shifts.

AuthorsOpenReview ↗

Response to Reviewer 8CDg [2/2]

4. Direct evaluation of gradient reliability

Spearman correlation and RMSE do not directly measure gradient reliability. Section 4.5 and Appendix E.4 acknowledge this limitation. Appendix Table 13 examines synthetic oracle-gradient preservation, rather than alignment of a learned surrogate with the oracle.

The quantity ∥Qρ∇sθ(x)∥\lVert Q_\rho\nabla s_\theta(x)\rVert measures the removed gradient component, but its magnitude alone cannot tell us whether the remaining direction is better. We therefore evaluated the alternative diagnostic suggested by the reviewer: alignment with oracle finite-difference directions.

Additional surrogate–oracle alignment experiment. We compared raw and projected gradients of the same trained surrogate at identical evaluation points against oracle finite-difference directions. The evaluation used five matched seeds, held-out designs and optimization-trajectory points, and centered finite differences with step-size sensitivity checks. Cosine similarities were averaged within each seed before aggregation. Oracle information was used only for this post-hoc evaluation, never during training or candidate optimization.

Table R2. Surrogate–oracle gradient cosine similarity (mean ± SD).

TaskRaw gradientProjected gradient
Ant0.47 ± 0.070.62 ± 0.06
D'Kitty0.42 ± 0.080.59 ± 0.07
Superconductor0.39 ± 0.070.54 ± 0.06

Results are reported as mean ± standard deviation across five seed-level averages.

Projected gradients show higher mean cosine similarity on all three tasks. Because the surrogate and evaluation points are held fixed, the comparison isolates the effect of projecting the gradient. The improvement concerns local alignment; final oracle performance remains a separate question.

5. Notation

We will clarify the notation in Section 2 by explicitly defining V=(v1,…,vm)V=(v_1,\ldots,v_m) as either YY or ZZ and distinguishing each vector from its scalar components.

Reviewer_8CDgOpenReview ↗

Response to Author Rebuttal

Thank you for the detailed response and additional experiments. The TF-Bind-10 component ablation and the surrogate–oracle gradient-alignment results address important parts of my original questions.

My remaining reservation concerns the strength of the connection between the training objective and the claimed search benefits. The trajectory bound is conditional, its assumptions do not follow from the consistency loss, and it does not establish improvement in the true objective. The new alignment experiment provides relevant empirical support for gradient projection, but does not by itself establish how much the training-time consistency term contributes to this improvement or when the shared spectral bias will be beneficial.

Overall, the rebuttal strengthens the empirical case, and I continue to find the distinction between ranking quality and search-direction reliability useful. However, the theoretical support remains limited and the absolute gains over strong ranking baselines are modest. I therefore maintain my rating of 3 for now.

Reviewer_GK2rOpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

This paper proposed a new method for offline model-based optimization, by aligning their score models in the original input space with an induced low-frequency space. However this method is nonsense and the experimental evaluation is inappropriate.

Critical strengths

None

Critical weaknesses
  1. Inappropriate experimental evaluation protocol : I believe that all the baseline results on Table 1 were copied directly from the learning to rank paper [4]. As shown in various prior works, these performances could be changed across different systems. However the author did not provide any baseline re-run results. This made an unacceptable, effortless and unreliable experimental results from the authors.

  2. Completely lacking the discussion with a crucial approach in offline model-based optimization : generative modeling. There were various method in generative modelings such as [1],[2],.., what is the advantage of this proposed method compared to the generative approach ?
These experiment results are also lacking of crucial sota baselines such as [1],[3],[5].

  3. Overall, the method is nonsense. There is no reasonable explanation why we need to train our score models in two input spaces and aligning it together. The author did not provide a clear motivation to that why we need to introduce the low-frequency design spaces. Figure 1 is also nonsense and did not provide any intuition supporting the proposed method. The claim for stable gradient search is not sound and also does not have any practical evidences. Transforming the original design space to a ow-frequency design space may even introduce some missing information to recover the original design space.

  4. Mismatch between the proposed training and search: The training process use the low-frequency in design space but the searching process use the low-frequency in gradient of score model’s space . During the training, the author introduced the low-frequency space PρxP_\rho x to train their score models, but eventually they applied PρP_\rho to the gradient of xtx_t as Eq (12). Why don’t the author use ∇sθ(Pρxt)\nabla s_\theta(P_\rho x_t) to align with their proposed training?

  5. Eq (12) is not novel : [6] already introduced a RL-approach to learn the matrix that changed the gradient directions with reasonable explanation. But in this paper, the author wrote the Conditional trajectory analysis which is completely not sound to support their proposed search. This section is basically about the gap between common gradient search and their proposed gradient search. But what is the reason to show this here? Why do we need to propose a new gradient search process but then showing the gaps with the normal gradient search? How this help to the increasing in final performance?

  6. Multiple mismatch in technical presentations, I suspect that this is highly artificial LLM- generated contents. The transformation PρP_\rho was wrote as matrix multiplication in multiple equations but it turns out as FFT in Eq (4). Eq(3) introduced some unreasonable conditions. Eq after Eq (12) could also lead to a nonsense condition xt+1=xtx_{t+1}=x_{t} . The pseudo-code in appendix have "Apply a feasible-domain projection if required by the task", but there is nothing to do with this as Eq (12) taking gradient of score models with respect to the input in original design spaces.

I suggest clear rejection for this paper and there is no chance for this since the author conducted effortless inappropriate experiments and provided nonsense method.



References :

[1] ROOT: Rethinking Offline Optimization as Distributional Translation via Probabilistic Bridge

[2] Diffusion Models for Black-Box Optimization

[3] Design Editing for Offline Model-based Optimization

[4] Offline Model-Based Optimization by Learning to Rank

[5] Generative adversarial model-based optimization via source critic regularization.

[6]Offline Model-Based Optimization via Policy-Guided Gradient Search

Questions for authors

See Weakness

4 comments
AuthorsOpenReview ↗

Response to Reviewer GK2r [1/3]

We appreciate the detailed review. We address the baseline and comparison questions first, then clarify the projection and its role in search. We also report new baseline reruns, projection controls, and gradient-direction experiments.

1. Baseline provenance and reproducibility

The source of each baseline result should be explicit. The baseline rows in Table 1, including RaM-ListNet and RaM-RankCosine, are reported as published by Tan et al. (2025; eight seeds), following common Design-Bench practice for comparability with prior work. We should have made this clear in Table 1. Published results also cannot rule out differences between software environments.

To address this directly, we reproduced both ranking baselines in our own environment, using the same datasets, normalization, initialization, and 128-candidate budget as SASS, with five seeds matched to the SASS runs.

Table R1. Baseline reproduction in our environment.

MethodPublished mean (Tan et al., 2025)Our rerun, mean ± SD
RaM-ListNet0.8160.815 ± 0.004
RaM-RankCosine0.8120.813 ± 0.005
SASS—0.827 ± 0.003

Five seeds. Standard deviations are computed across seed-level task averages.

The rerun means differ from the published means by 0.001 for both methods, and SASS remains higher than the rerun baselines by 0.012 and 0.014 on average. The ranking-baseline comparison therefore gives a similar result with either published or rerun numbers. Other baselines in Table 1 remain literature-sourced. In the revision, we will mark the provenance of every Table 1 row, add the rerun results, report paired seed-level comparisons against these reruns, and provide the corresponding run configurations.

2. Generative MBO comparisons

Section 4.1 and Table 1 include the following generative and backward-design methods: CbAS, MINs, DDOM, BONET, and GTG. In particular, the reviewer's reference [2], Diffusion Models for Black-Box Optimization, is DDOM (Krishnamoorthy et al., 2023). In Table 1, SASS attains a higher mean score than each of these five methods on all five tasks, although their numbers are literature-sourced. Appendix A also discusses generative design methods. We will make this coverage clearer in the related-work discussion.

The comparison does not cover every method the reviewer mentions, notably ROOT, Design Editing, and the source-critic-regularized generative approach. This limits the scope of our comparison with generative MBO. Our controlled experiments instead examine the effect of sharing a structural constraint across representation, preference learning, and search. Component ablations and the controls below test that design choice.

AuthorsOpenReview ↗

Response to Reviewer GK2r [2/3]

3. Motivation for low-frequency projection and information preservation

Section 3.1 presents low-frequency projection as a representation-dependent inductive bias. The motivation is that preserving rankings on observed designs does not determine the gradient directions encountered during search. SASS uses one retained subspace to connect the surrogate's input views, preference consistency, and allowed update directions.

The method does not replace every design with its low-frequency projection. Eq. (5) uses one dual-branch surrogate with access to both xx and PρxP_\rho x. As clarified in Appendix B.2, C2 evaluates this same entire surrogate at xx and PρxP_\rho x; it does not train two independent score models. Eqs. (8)–(11) explain how this consistency constrains relative score changes across the two views, without implying a uniform gradient bound. At search time, Eq. (12) projects the update direction, so before feasibility projection or decoding,

Qρxt+1=Qρxt.Q_\rho x_{t+1}=Q_\rho x_t.

The update therefore preserves the component outside the retained subspace, but cannot search along those directions. This restriction can be harmful when the removed directions contain important information. Appendix Table 13 and Appendix F explicitly document this limitation. Figure 1 illustrates how the same projection connects input views, preference consistency, and update directions; its caption explicitly labels the B4 trajectories as schematic. Empirical support comes from the component ablations and the additional comparisons below.

The submitted Appendix Table 8 reports a mean score of 0.827 at ρ=0.7\rho=0.7, compared with 0.776 under aggressive filtering (ρ=0.1\rho=0.1), indicating that the retained subspace matters. To assess whether the benefit is attributable to Fourier projection rather than model capacity or generic subspace restriction, we added capacity-matched and rank-matched controls.

Table R2. Controlled projection comparisons (mean ± SD).

ConfigurationMean score ↑
Capacity-matched, no projection0.820 ± 0.004
Random orthogonal projection0.819 ± 0.005
PCA projection0.821 ± 0.004
SASS (Fourier)0.827 ± 0.003

Results are reported as mean ± standard deviation across five matched seeds. Projection-based controls use identical retained rank, architecture, and search budget. Model capacity is matched for the no-projection control. PCA is fitted using offline training inputs only.

SASS has the highest mean among these controls. The paired improvement over PCA is +0.006, with a 95% confidence interval of [0.002, 0.010]. Fourier projection performs best among these controls, although its advantage may depend on the representation and objective.

4. Input projection during training and gradient projection during search

For x∈RDx\in\mathbb{R}^D, the input gradient ∇xsθ(x)∈RD\nabla_x s_\theta(x)\in\mathbb{R}^D is indexed by the same input coordinates. Applying PρP_\rho to it selects update directions in the same retained coordinate subspace used for the input views. As Section 3.1 explains, this is a projection in input-coordinate space, not a Fourier transform of the scalar scores or the surrogate function.

C2 and C3 use the same subspace for different purposes: C2 encourages preference agreement between sθ(x)s_\theta(x) and sθ(Pρx)s_\theta(P_\rho x), while C3 restricts ascent of the original surrogate to that subspace. The two operations are distinct. For an orthogonal projector, the chain rule gives

=P_\rho\nabla s_\theta(P_\rho x),$$ which generally differs from $P_\rho\nabla s_\theta(x)$. The chosen update has the constrained interpretation already provided in Eq. (13): $$\arg\max_{\delta\in\mathrm{range}(P_\rho)} \left\lbrace \nabla s_\theta(x)^\top\delta - \frac{\lVert\delta\rVert^2}{2\eta} \right\rbrace = \eta P_\rho\nabla s_\theta(x).$$
AuthorsOpenReview ↗

Response to Reviewer GK2r [3/3]

4. Input projection during training and gradient projection during search (continued)

Eq. (13) explains the chosen update as constrained ascent of the original surrogate. To assess the reviewer's proposed alternative empirically, we compared the following directions using the same trained surrogate at identical evaluation points:

  1. Raw gradient, ∇sθ(x)\nabla s_\theta(x).
  2. Projected gradient at the original input, Pρ∇sθ(x)P_\rho\nabla s_\theta(x).
  3. Gradient through the projected input, Pρ∇sθ(Pρx)P_\rho\nabla s_\theta(P_\rho x).

Table R3. Oracle-gradient cosine alignment (mean ± SD).

TaskRaw gradientP∇s(x)P\nabla s(x)P∇s(Px)P\nabla s(Px)
Ant0.47 ± 0.070.62 ± 0.060.57 ± 0.06
D'Kitty0.42 ± 0.080.59 ± 0.070.54 ± 0.07
Superconductor0.39 ± 0.070.54 ± 0.060.50 ± 0.06

Same experiment as Table R2 in our response to Reviewer 8CDg, with the additional Pρ∇sθ(Pρx)P_\rho\nabla s_\theta(P_\rho x) direction. Results are reported as mean ± standard deviation across five matched seeds. Standard deviations are computed across seed-level means. Oracle gradients are estimated post-hoc using centered finite differences at held-out and search-trajectory points, with finite-difference step-size sensitivity checks.

Our update, Pρ∇sθ(x)P_\rho\nabla s_\theta(x), has the highest mean cosine similarity with the estimated oracle gradient on all three tasks. Its pooled paired improvement over Pρ∇sθ(Pρx)P_\rho\nabla s_\theta(P_\rho x) is +0.047, with a 95% confidence interval of [0.025, 0.069]. This favors our chosen direction in the local alignment test, rather than establishing a difference in final optimization outcomes. Oracle information was used only for post-hoc evaluation, never during training or search.

5. Novelty and the role of the trajectory analysis

Changing a gradient direction is not, by itself, novel. PGS learns a state-dependent coordinate-wise step-size vector through offline RL, corresponding to diagonal gradient preconditioning. SASS instead uses a fixed orthogonal spectral projector shared across surrogate architecture (C1), preference consistency (C2), and search (C3). The contribution lies in this shared formulation, not in Eq. (12) alone. PGS is already cited in Section 4.1 and included in Table 1 as a literature-sourced comparison; we will make the methodological distinction clearer. Appendix Table 9 reports means of 0.827 for Full SASS and 0.822 for C3 alone, while the rerun ranking baselines in Table R1 average 0.815 and 0.813. Together, these results motivate evaluating the full formulation; Table R2 separately controls for capacity and subspace choice.

The trajectory analysis is not a proof of performance improvement. Section 3.3 and Appendix C.4 characterize finite-horizon deviation from unprojected surrogate ascent under explicit assumptions. A small discrepancy is not itself a reason to prefer projected search, and the bound does not guarantee oracle improvement or automatically apply to the ReLU implementation. We will distinguish these roles more clearly: the bound characterizes conditional trajectory geometry, the optimization experiments measure final outcomes, and Table R3 measures local gradient alignment.

6. Projection properties, stationarity, feasibility, and LLM disclosure

  • Matrix and FFT formulations: Eq. (3) gives the properties of an orthogonal projector. Eq. (4) implements this linear operator with rFFT, a fixed binary mask, and irFFT, without constructing a dense matrix. These are compatible descriptions of the same projection.
  • Stationarity: If Pρ∇sθ(x)=0P_\rho\nabla s_\theta(x)=0, Eq. (12) can produce xt+1=xtx_{t+1}=x_t. This is stationarity within the retained subspace, and need not be full-space or oracle optimality.
  • Feasibility: Algorithm 1 applies a feasible-domain projection after the spectral gradient update when required. This is a separate constraint-enforcement step. The stated trajectory bound concerns updates before this operation and discrete decoding.
  • Assumptions: The smoothness and complementary-gradient assumptions are conditional and do not follow automatically from ranking consistency.

Appendix G discloses ChatGPT assistance with manuscript organization, wording, figure-editing instructions, and mathematical explanations. No experimental measurements were generated through this assistance. The authors remain responsible for the derivations, experimental results, and scientific claims.

Reviewer_GK2rOpenReview ↗

Response to Author Rebuttal

  1. Who told you that copying results from other's published paper is common practice for prior comparison in offline model-based optimization? This SASS paper copied not only RaM results but also all other baseline results from RaM.

I have enough experience in this community and know that authors in other well published papers such as RaM , ROOT, did re-run their baseline in their own system instead of copying.

  1. The discussion for related works in appendix is highly insufficient, discussion with recent generative methods such as ROOT , DEMO is important. This paper does not show any advantages compared to the generative approach.

Please survey literature carefully before doing your work.

For other technical things, these responses are still highly insufficient and do not address my concerns.

There is still no clear mathematical reason why the proposed low-frequency would help stabilize the optimization process. There is still a technical mismatch: during training, the method retrained a projected input space along with original space, while during optimization, it projects the gradient. Again, there is no mathematical or conceptual justification for why these training and search procedures need to be used together in this form, or why the projection used during training would benefit the projection used during search. All conceptual explanation by the authors are imagine, not a mathematical justification with soundness. The proposed method totally does not make sense.

Once again, even the author acknowledged their AI usages, but this submission is far below the quality required for acceptance with too many hallucinated contents.

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

The paper proposes SASS for offline model-based optimization, arguing that accurate ranking alone does not guarantee reliable gradient directions outside the training distribution. SASS applies one low-pass FFT projection in three places: a dual-branch surrogate on original and projected inputs, a ranking-consistency loss between the two views, and gradient updates projected onto the low-frequency subspace. On five Design-Bench tasks, it achieves state-of-the-art results in terms of the mean rank.

Critical strengths
  • Clear motivation: good ranking on observed designs does not determine the surrogate’s gradient geometry during search.
  • Simple, consistent design that shares one projection between learning and search, with a clean analysis of what the consistency loss constrains.
Critical weaknesses
  • The FFT is applied along the feature index of the input vector, which has no natural ordering for tabular designs (e.g., Superconductor features, morphology parameters) or flattened logits.
  • The robustness experiment is somewhat circular. Noise is injected into exactly the subspace that SASS removes by design, so reduced degradation is expected, and the test is limited to Superconductor.
Questions for authors
  • Please justify the use of FFT on tabular designs. How does performance change under a random permutation of the feature order before the FFT?
  • How about directly add Gaussian noise into the input to evalute the robustness of SASS? Moreover, it would be better to conduct robustness analysis on different benchmarks.
2 comments
AuthorsOpenReview ↗

Response to Reviewer vgPw [1/2]

We appreciate the reviewer’s comments on SASS’s motivation and unified design. The questions about feature ordering and robustness are important. We address them with new feature-permutation, random-subspace, and Gaussian-noise experiments, together with the controls in the submitted paper.

Q1. FFT justification and feature-order sensitivity

Tabular features have no canonical ordering, so Fourier projection is a representation-dependent modeling choice. Section 3.1 and Appendix F do not assume that low-frequency modes are meaningful for every representation. We use the Fourier subspace because it provides an efficient, common constraint for surrogate representation (C1), preference consistency (C2), and search (C3). Its usefulness is ultimately an empirical question.

The submitted paper provides two relevant diagnostics: Appendix Table 8 reports mean scores of 0.825–0.827 for moderate retention (ρ=0.5\rho=0.5–0.90.9), versus 0.776 under aggressive filtering (ρ=0.1\rho=0.1); Table 5 reports oracle rank correlations of 0.850, 0.940, and 0.920 at ρ=0.7\rho=0.7 on Superconductor, TF-Bind-8, and TF-Bind-10. These results motivate the selected projection settings, but leave the effect of feature ordering open.

Additional permutation and random-subspace experiments. We evaluated 20 independent random feature permutations with five matched seeds per task. Each permutation Π\Pi was applied consistently during training and search, corresponding to

Pρ(π)=Π⊤PρΠ.P_\rho^{(\pi)}=\Pi^\top P_\rho\Pi.

Oracle evaluation preserved the original feature semantics. We also evaluated random orthogonal projectors with the same retained rank, architecture, and training/search protocol to compare Fourier projection with generic subspace restriction.

Table R1. Feature-order and projection sensitivity.

TaskOriginal SASSPermuted SASSRandom projectorPaired drop, 95% CI
Ant0.969 ± 0.0260.966 ± 0.0030.957 ± 0.0040.003 [0.002, 0.004]
D'Kitty0.975 ± 0.0120.972 ± 0.0030.965 ± 0.0040.003 [0.002, 0.004]
Superconductor0.521 ± 0.0120.519 ± 0.0020.516 ± 0.0030.002 [0.001, 0.003]

Original SASS: standard deviation across five seeds. Permuted SASS and random projector: standard deviation across 20 projection-level seed means. Paired drop denotes the original-minus-permuted performance difference, with 95% confidence intervals computed from paired comparisons.

Permutation changes the mean score by just 0.002–0.003. Both Fourier variants also outperform the matched-rank random projectors on all three tasks. Thus, the gains are not tied to a single feature ordering in these tests. This is evidence of limited sensitivity to the permutations examined, not a claim of permutation invariance or universal optimality.

AuthorsOpenReview ↗

Response to Reviewer vgPw [2/2]

Q2. Gaussian noise and robustness across benchmarks

Table 4 includes matched-norm random, low-frequency, and high-frequency perturbations on Superconductor. Under random perturbations, the score drops are 0.026 for SASS and 0.036/0.037 for RaM-ListNet/RaM-RankCosine. The separation is largest under high-frequency corruption (0.018 versus 0.047/0.048) and smaller under low-frequency corruption (0.044 versus 0.046/0.047). These controls cover more than high-frequency-targeted noise, although they concern only one task. We therefore extended the evaluation.

Appendix Table 10 reports component-level results at high-frequency corruption severity 0.20: the drops for Base, C1, C2, C3, and Full SASS are 0.047, 0.028, 0.027, 0.046, and 0.018. C3 alone has a drop similar to Base, while C1 and C2 reduce degradation. The reductions from C1 and C2 indicate that robustness in this setting is not explained by search-time filtering alone.

Additional Gaussian-noise experiment. Following the reviewer's suggestion, we evaluated independent isotropic Gaussian training-input corruption on all five benchmarks:

\epsilon\sim\mathcal{N}(0,\sigma^2I),\qquad \sigma=\frac{0.20}{\sqrt{D}}.$$ Here, $D$ is the flattened representation dimension, giving an expected squared perturbation norm of $0.20^2$. Noise was applied to normalized continuous inputs or continuous TF-Bind logits, not categorical token IDs. All methods used the same corruption protocol and five matched seeds; the oracle itself was not perturbed. **Table R2. Gaussian training-input robustness ($\sigma=0.20/\sqrt{D}$).** | Task | SASS drop ↓ | Ranking baseline drop ↓ | |---|---:|---:| | Ant | **0.031 ± 0.007** | 0.047 ± 0.009 | | D'Kitty | **0.028 ± 0.006** | 0.041 ± 0.008 | | Superconductor | **0.028 ± 0.005** | 0.037 ± 0.007 | | TF-Bind-8 | **0.018 ± 0.004** | 0.029 ± 0.006 | | TF-Bind-10 | **0.039 ± 0.008** | 0.059 ± 0.010 | | **Mean** | **0.0288** | **0.0426** | *Values represent mean ± standard deviation across five matched seeds for clean-to-noisy score drops. The ranking baseline denotes the stronger ranking method on each task.* SASS degrades less on all five tasks. Its average drop is 0.0288, compared with 0.0426 for the ranking baselines—a 32.4% relative reduction. Unlike the targeted perturbations, isotropic Gaussian noise is not confined to the removed frequency subspace. The result therefore broadens the robustness evidence, although it does not address arbitrary distribution shifts.

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