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Under review as a conference paper at ICLR 2027

State-Adaptive Multi-Scale Search for Scalable Bayesian Optimization

Abstract

Bayesian optimization (BO) is attractive for expensive black-box problems, but exact Gaussian-process (GP) inference scales as in the number of observations and high-dimensional search introduces a separate statistical and optimization challenge. These pressures are acute in robotics and other costly tuning settings: reusable hyperparameter histories may initially be small because each trial is expensive, yet a sequential campaign can rapidly accumulate hundreds or thousands of observations. We introduce Adaptive Multi-Scale Dirichlet-Guided Variational Gaussian Process (\method), a scalable sparse-GP BO method that combines variational inference with state-adaptive spatial allocation. Beyond the usual incumbent-centered exploitation and uncertainty-driven exploration signals, a Dirichlet-process mixture summarizes promising occupied modes and provides an additional data-driven search center. Across six synthetic benchmarks spanning 2–500 dimensions and 500–5000 total evaluations, achieves the best mean endpoint result among the three directly compared methods on every task, reducing final regret relative to adaptive-depth FocalBO by on average. It also obtains the best final objective on 11-D HalfCheetah and the 32-D FrankaBell manipulation task. Algorithm analysis shows that the controller uses all four search actions and that its high-dimensional gains persist throughout the optimization trajectory rather than appearing only at the endpoint. Recorded wall-clock cost across the eight retained tasks is about lower than adaptive-depth FocalBO, while an acquisition study shows robust performance under TS, UCB, and EI.

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
Bayesian Optimization

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Paper summary

This paper presents a scalable BO method, abbreviated “AMS-DVGP”. The authors distinguish “scalable” as meaning both in the number of observations (computational efficiency) and the number of dimensions (optimization efficiency). AMS-DVGP builds on the existing SVGP literature and adds on a “controller” that changes the search center, spatial scale, local/global behavior, and batch allocation. It also uses a Dirichlet-process Gaussian mixture summarize clusters of previously observed locations.

Critical strengths

The reported performance leadership over FocalBO is consistent

Trajectory-averaged regret is an interesting idea to measure early performance

Critical weaknesses

AMS-DVGP and FocalBO both share the same "improve BO performance by focusing SVGP training on local regions by weighting training data according to the active search region and using several levels of locality". The authors claim they differ by the controller by adding local/global search, choosing the centers, and batch allocation. Thus, the primary novelty introduced by this paper appears to be the integration of these ideas.

Unfortunately, several details are hidden inside a sparse Section 3.3. While Appendix A.2 gives the relevant hyperparameters, the paper itself offers no explanation as to how these parameters are chosen, how sensitive they are, and to what extent they are responsible for the experimental results.

For example, if we change the multi-scale allocation to (0.2, 0.4, 0.4), do we still preserve the performance gain and why? Some ablations to study how each piece of these ideas contribute to the performance of the method would help strengthen the paper.

The ingredients proposed lack significant details, handling, and justification. For example, take Section 3.2 on the progress. Here, progressed is classified into one of four categories. There is no explanation how this is done so. The appendix only offers hyperparameters. Even then, the threshold defines a Δt\Delta_t which is nowhere else found in the paper.

Equation 1 is the standard ELBO for SVGPs which sums the log-likihood terms and adds a KL penalty. However, Equation 4 uses a weighted average, so there is an implicit nn scaling for the penalty.

Questions for authors

Figure 5 shows that the method is “robust” against choosing among UCB/EI/TS. In standard BO procedures vary due to inherent differences in locality bias and how the acquisition functions are optimized. e.g. TS is often quite exploratory and EI is often exploitative. While the paper makes no comment on this, it is not clear whether such a property is desirable or why such a behavior manifests in the approach. Some questions I ask are: are all acquisitions inherently local? One can answer this by sweeping the βt\beta_t parameter in UCB, for example, and measuring the distance between two queries, between the query and the incumbent, etc.

How does the asymptotic complexity of your method compare to FocalBO or SVGPs? I have a feeling the full-covariance DP-GMM has a large effect on this.

Figure 4 shows that despite different objective functions and dimensions, the approach spends roughly the same time in each of the four categories the authors have binned. Is there an explanation, despite the different landscapes, the behavior is similar?


I think [1] is a very related paper, but since it was only released the start of this year I would consider it as concurrent work. I bring this up only to make authors aware of it for future versions of this work.

[1] Zhang, Yan, et al. "Regime-Adaptive Bayesian Optimization via Dirichlet Process Mixtures of Gaussian Processes." arXiv preprint arXiv:2601.20043 (2026).

9 comments

Thank you for the specific suggestions on allocation, acquisition locality, computational cost, and related work. We have expanded the method specification, completed the targeted experiments, and narrowed the claims where the evidence does not support a stronger conclusion.

Q1. Given the overlap with FocalBO, what is the specific contribution of AMS-DVGP, and how does it differ from the concurrent DP-mixture work of Zhang et al.?

A. We agree that local weighting of sparse-GP training and a hierarchy of spatial scales are shared with FocalBO. We now present our contribution as a specific integration for adaptive spatial allocation. FocalBO adapts the depth of an incumbent-centered hierarchy; AMS additionally chooses local/global actions, can use a ranked cluster of visited inputs as a center, and allocates the next batch across regions and scales. Section 2 explicitly acknowledges these shared ingredients.

Thank you also for pointing us to Zhang et al., Regime-Adaptive Bayesian Optimization via Dirichlet Process Mixtures of Gaussian Processes. We have cited and discussed this work in a dedicated related-work subsection. RAMBO uses a DP mixture of GPs to represent latent objective regimes, with separate GP components. AMS uses one SVGP to predict the objective and a separate DP-GMM over visited input locations to guide proposals. Its progress categories describe improvement during a run, rather than latent components of a mixture predictive model. This is a distinction in modeling and decision roles, not a performance comparison with RAMBO; no head-to-head superiority is claimed. [Zhang et al., arXiv:2601.20043]

AspectFocalBORAMBO (Zhang et al.)AMS-DVGP
Objective surrogateSparse GP with focalized trainingDP mixture of GP componentsOne SVGP
Main adaptive objectDepth of an incumbent-centered hierarchyLatent objective regime / mixture componentLocal/global action, center, scale, and batch allocation
Role of mixture structureNot the AMS DP-GMM mechanismPredictive model and acquisition distributionSeparate DP-GMM over visited input locations; observed responses rank occupied clusters for proposal centers
Scope of our claimShared ingredients are acknowledgedModeling-role distinction onlyNo head-to-head superiority claim over RAMBO

These distinctions are discussed in Sections 2.3-2.4.

Q2. How were the controller parameters selected, how sensitive are the results to them, and does the performance gain persist if the multi-scale allocation is changed to (0.2,0.4,0.4)?

The controller constants were engineering choices reused across all eight tasks without task-specific controller tuning. We now state this explicitly, rather than suggesting that the particular numerical values were theoretically derived or selected by a validation sweep. Section 3 and Appendix A.2 define the progress statistic, thresholds, cluster gate, scale tuples, action priorities, and integer allocation rule. For example, the raw-incumbent progress statistic is Δt=(bt−bt−1)/∣bt−1+10−8∣\Delta_t=(b_t-b_{t-1})/|b_{t-1}+10^{-8}|, with thresholds 0.01, 0.003, and 0.001. The fourth accumulated stagnation event triggers global escape. We also explain the controller's sensitivity to response transformations.

We tested your proposed fine/medium/coarse allocation (0.2, 0.4, 0.4) on both 500-D tasks, with ten matched seeds and the original evaluation budgets and inducing capacities.

The endpoint reductions are 28.7% and 85.7%; all four paired comparisons have Holm-adjusted pH=0.0078p_H=0.0078 (Table 11). The initial response prefixes match for all twenty pairs. The archived files establish initial-y matching; the new controls additionally retain complete initial-X checks. Because these runs span execution environments, this comparison concerns evaluation efficiency.

Against the new full AMS baseline with the original allocation, the alternative allocation has raw p-values from 0.1602 to 0.3223, with all four adjusted values equal to 0.6406 (Table 10). Thus the observed advantage over archived FocalBO persists for the tested alternative; these tests do not prove equivalence between allocations or robustness to all controller constants. Both allocations retain all three scales, but that design rationale is not an experimentally isolated explanation. The remaining thresholds have not been exhaustively swept.

We also completed fixed-mixture and likelihood-only controls (Figure 8). They require more limited attribution: on Rosenbrock the fixed mixture has worse mean endpoint and trajectory regret, but its raw p=0.0137p=0.0137 adjusts to 0.1094; the likelihood-only control is close to full AMS. The revised text distinguishes these interventions from the archived removal of the complete training mechanism.

The suggested allocation changes fine/medium/coarse shares from (0.4, 0.4, 0.2) to (0.2, 0.4, 0.4). The two relevant paired comparisons are reproduced together below; Rosenbrock values are in millions.

Task / metricFull AMS 40/40/20Suggested 20/40/40Raw pp vs fullpHp_H vs fullArchived FocalBOpHp_H vs FocalBO
Rastrigin endpoint4703.14852.00.23240.64066803.20.0078
Rastrigin trajectory5363.75550.30.16020.64067220.80.0078
Rosenbrock endpoint1.3741.5610.16020.640610.9210.0078
Rosenbrock trajectory4.5674.9580.32230.640616.6780.0078

Controller definitions are in Sections 3.1-3.3 and Appendix A.2, Table 4; complete paired results are in Appendix F.2, Tables 10-11 and Figure 8.

Q3. Why does Eq. (4) use a weighted average of the likelihood terms, which appears to introduce an implicit NN-dependent scaling of the KL penalty relative to Eq. (1)?

A. Your observation about the submitted expression is correct. Averaging the likelihood while retaining full KL gives ∑iℓi/N−KL\sum_i\ell_i/N-\mathrm{KL}, which is equivalent up to scale to ∑iℓi−NKL\sum_i\ell_i-N\mathrm{KL}. The written equation omitted the KL/N normalization used in the augmented training implementation.

The corrected Eq. (4), under equal weights and no auxiliary terms, gives ∑iℓi/(N+ε)−KL/N\sum_i\ell_i/(N+\varepsilon)-\mathrm{KL}/N. Omitting the stabilizer yields the standard ELBO divided by N. N denotes the total training-set size, including during minibatch training. Appendix F.6 additionally compares both normalizations on fixed histories and reports prediction error, latent/predictive standard deviations, coverage, and UCB selections. We explicitly report predictive overcoverage under KL/N and do not claim that this equal-weight diagnostic establishes calibration of the complete weighted model.

The fixed-history diagnostic is:

NNPenaltyRMSELatent SDPredictive SD95% coverageNLPD
100KL/NN0.9601.5332.2410.99961.807
100KL4.4411.3863.7390.97982.939
300KL/NN1.3221.7432.6580.99452.030
300KL7.1671.7594.7550.90223.617

See Section 3.5, Eq. (4), and Appendix F.6, Table 15 and Figure 11.

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Paper summary

The paper proposes AMS-DVGP, which combines sparse variational Gaussian processes with state-adaptive regional search to address growing observation counts and high-dimensional search in Bayesian optimization. Based on recent optimization progress, the method switches among information-guided search, multi-scale probing, cluster contraction, and global escape, while a Dirichlet-process Gaussian mixture provides alternative search centers beyond the incumbent. During training, observation likelihoods are weighted using posterior uncertainty and affinity to active search regions, coupling surrogate fitting with regional search. Across six synthetic benchmarks and two robotic simulation tasks, the method achieves better mean endpoint results than adaptive-depth FocalBO and SVGP, with additional trajectory-averaged regret and runtime analyses assessing optimization efficiency.

Critical strengths
  1. Clear modular search design: Separating candidate-region generation from acquisition selection allows historical clustering and state switching to adapt search centers, scales, and batch allocation, extending regional search beyond the incumbent's neighborhood.

  2. Well-controlled experimental comparisons: The main experiments use TS across methods and seed-matched initial designs over ten paired runs, reporting both endpoint performance and trajectory-averaged regret to demonstrate sustained improvements over the two baselines.

Critical weaknesses
  1. Insufficient justification of the training objective: Equation (4) averages the likelihood terms while retaining the full KL penalty, changing the observation-count-dependent data–prior balance relative to Equation (1), without analyzing its effects on posterior uncertainty and acquisition decisions.
  2. Incomplete controller specification: Sections 3.2–3.3 and Algorithm 1 do not fully specify the recent-improvement statistic, cluster-gating score, or multi-scale radii, making key search decisions difficult to reproduce independently from the paper's description.
  3. Insufficient component-level evidence: The strategy proportions and overall regret comparisons in Section 4.6 do not isolate the contributions of state adaptation, DP clustering, and likelihood weighting, leaving the observed gains insufficiently attributed to these individual designs.
Questions for authors
  1. Training objective justification: Could the authors derive the relationship between Equations (4) and (1) under equal weights and no auxiliary regularization, and justify the observation-count-dependent relative KL weighting and its implications for posterior uncertainty?

  2. Controller specification and scale consistency: Could the authors fully define the improvement statistic, cluster-gating score, and multi-scale radii, and analyze whether the transformation f(x)↦af(x)+bf(x)\mapsto af(x)+b, with a>0a>0, changes controller regime assignments at identical observation locations?

  3. Individual component contributions: Could the authors separately evaluate a fixed strategy mixture, removal of cluster guidance, and equal-weight training under matched initializations, evaluation budgets, and surrogate capacities, reporting endpoint and trajectory-averaged regret to isolate each component's contribution?

3 comments

Thank you for identifying the normalization issue and for specifying the controller details and component controls needed to assess the method. We have corrected the equation, expanded the implementation description, and completed the requested targeted controls. We address each point below.

Q1. What is the relationship between Eqs. (4) and (1) under equal weights and no auxiliary regularization, and what are the implications of the relative KL scaling for posterior uncertainty and acquisition decisions?

A. Your reading of the submitted equation is correct. Let ℓi=Eq(fi)[log⁡p(yi∣fi)]\ell_i=\mathbb{E}_{q(f_i)}[\log p(y_i\mid f_i)]. Under equal weights and no auxiliary regularization, the submitted expression, omitting the numerical stabilizer, was

1N∑iℓi−KL[q(u)∥p(u)].\frac{1}{N}\sum_i\ell_i-\mathrm{KL}[q(u)\Vert p(u)].

Multiplying this expression by NN gives ∑iℓi−NKL\sum_i\ell_i-N\mathrm{KL}, so it changes the data–prior balance relative to Eq. (1). This was an error in the written equation. The augmented training implementation normalizes the KL term by the total observation count NN.

The revised Eq. (4) and its accompanying derivation now state that, with unit weights and auxiliary terms removed, the implemented full-batch objective is

-\frac{\mathrm{KL}[q(u)\Vert p(u)]}{N}, \qquad \varepsilon=10^{-7}.$$ Omitting the stabilizer yields $\mathcal L_{\mathrm{SVGP}}/N$, which is Eq. (1) up to a positive scale at fixed $N$. In minibatch training, the weighted likelihood is normalized over the batch while the KL denominator remains the total training-set size. This equivalence is restricted to equal weights and no auxiliary terms; it is not a claim that the general weighted objective is the ordinary ELBO. To address the implications empirically, Appendix F.6 compares the two KL normalizations on fixed Ackley histories, using equal weights, no auxiliary terms, matched model initialization, 20 inducing points, and 200 full-batch Adam updates. At $N=100$ and $N=300$, using KL/N instead of full KL with a mean likelihood reduces mean held-out RMSE from 4.441 to 0.960 and from 7.167 to 1.322. Mean predictive standard deviations change from 3.739 to 2.241 and from 4.755 to 2.658 (Table 15). Figure 11 reports the associated fixed-candidate UCB selection behavior. We also report the limitation: nominal 95% predictive coverage under KL/N is 99.96% and 99.45%, indicating overcoverage on this design. The latent and predictive standard deviations have different patterns, so both are reported. These finite-training, equal-weight diagnostics demonstrate sensitivity to the normalization; they do not establish calibration of the full weighted AMS model. The completed new-run manifests were also checked against the six pinned algorithm-source hashes. The fixed-history, equal-weight diagnostic compares this implemented normalization with subtracting the full KL while retaining a mean likelihood: | $N$ | Penalty | RMSE | Latent SD | Predictive SD | 95% coverage | NLPD | |---:|---|---:|---:|---:|---:|---:| | 100 | KL/$N$ | 0.960 | 1.533 | 2.241 | 0.9996 | 1.807 | | 100 | KL | 4.441 | 1.386 | 3.739 | 0.9798 | 2.939 | | 300 | KL/$N$ | 1.322 | 1.743 | 2.658 | 0.9945 | 2.030 | | 300 | KL | 7.167 | 1.759 | 4.755 | 0.9022 | 3.617 | Both objectives are evaluated on the same 1024 held-out points within each seed. The corrected objective and derivation are in Section 3.5, Eq. (4); the diagnostic is in Appendix F.6, Table 15 and Figure 11.

Q2. Can the improvement statistic, cluster-gating score, and multi-scale radii be fully specified, and can objective transformations change controller regime assignments at identical observation locations?

A. Section 3 and Appendix A.2 now specify the following:

  • At the start of batch tt, btb_t is the best observed response in the raw maximization units. After initialization, Δt=(bt−bt−1)/∣bt−1+10−8∣\Delta_t=(b_t-b_{t-1})/|b_{t-1}+10^{-8}|. The first exceeded threshold among 0.01, 0.003, and 0.001 determines fast, steady, or slow progress; otherwise a nondecreasing incumbent is classified as stagnation.
  • The fourth accumulated stagnation event triggers global escape and resets the counter. Intervening progress does not reset it. Other stagnation events alternate the requested multi-scale and information-guided actions through the previous-action rule. Fast progress requests contraction subject to the cluster gate; a rejected gate falls back to information-guided search.
  • For the occupied cluster CC with the highest mean response, the gate is
\max_{i\in C}y_i-\operatorname{median}_{i\in C}y_i +\min(0.2,0.5|C|/N) -\min(0.1,0.1\operatorname{Var}_{i\in C}y_i) \right).$$ The variance uses divisor $|C|$. With at least ten observations, fast progress contracts around the cluster mean when $g_C>0.7$, using Gaussian scale 0.05 and unit-box clipping. Missing cluster information or fewer than three cluster members gives a zero gate score. - The fine/medium/coarse scales are (0.05, 0.20, 0.40) for $b_t>5$, (0.03, 0.12, 0.25) for $2<b_t\leq5$, and (0.01, 0.05, 0.15) otherwise. The default allocation is (0.4, 0.4, 0.2); the first two counts are rounded down and the last receives the remainder. Appendix A.2 also specifies candidate generation and the cluster-center inclusion condition. For the positive affine transformation $y'=ay+c$, the progress statistic becomes $$\Delta'_t= \frac{a(b_t-b_{t-1})} {|ab_{t-1}+c+10^{-8}|}.$$ Thus the controller is not invariant to arbitrary response shifts at identical observation locations. For example, 1 to 1.02 gives fast progress, whereas 101 to 101.02 gives stagnation. Pure positive rescaling preserves this ratio only when the numerical stabilizer can be neglected; moreover, the raw-response gate and scale thresholds can change under rescaling even if the progress label does not. Appendix F.3 quantifies this on fixed archived histories. A run-specific constant shift $c=0.9|b_0|$, fixed from initialization, changes 24/270 Rastrigin and 110/290 Rosenbrock pre-proposal regime labels. Doubling responses changes no labels in these histories. This is a replay of labels on fixed histories, not a new end-to-end BO experiment under transformed objectives. On fixed archived histories, the response-transform replay gives: | Transformation | Rastrigin labels changed | Rosenbrock labels changed | |---|---:|---:| | $y'=2y$ | 0/270 | 0/290 | | $y'=y+100$ | 1/270 | 0/290 | | $y'=y+0.9|b_0|$ | 24/270 | 110/290 | Complete replay results are reported in Appendix F.3.

Q3. Can the contributions of state adaptation, cluster guidance, and likelihood weighting be evaluated separately under matched initializations, evaluation budgets, and surrogate capacities?

A. We completed the requested fixed four-action mixture and likelihood-only controls on Rastrigin 500-D and Rosenbrock 500-D, each with ten seed-matched initial X/y, the same evaluation budget, TS, and inducing capacity. Each is compared with its own newly run full baseline. Removal of cluster guidance is covered separately by the archived matched ablation.

New configurationRastrigin endpoint / trajectory meanRosenbrock endpoint / trajectory mean
Full AMS4703.1 / 5363.71.374M / 4.567M
Fixed four-action mixture5195.4 / 5810.83.022M / 8.638M
Equal likelihood coefficients4878.2 / 5475.71.371M / 4.567M

The fixed mixture requests each action once per shuffled four-batch block, retaining internal gates and fallbacks. On Rosenbrock, both raw paired p-values are 0.0137, but both become pH=0.1094p_H=0.1094 in the eight-test family. The Rastrigin values are 0.1934, adjusted to 0.7734. Equal-likelihood comparisons have raw p-values from 0.1055 to 1 and do not establish a difference. Table 10 and Figure 8 report these results.

Removing DP guidance worsens both metrics on both tasks, with pH=0.0234p_H=0.0234 for each comparison in the archived twelve-test family (Table 6). We retain the less favorable archived results as well: the Rastrigin fixed-information endpoint comparison has raw p=0.0840p=0.0840, and that fixed policy has lower trajectory-averaged regret than full AMS on Rosenbrock despite a worse endpoint.

The archived approximately 14.7-fold Rosenbrock endpoint difference concerns replacement of the complete training mechanism. The new likelihood-only intervention preserves the other uses of weights, auxiliary terms, and base-training branch; it does not support attributing that large difference to the likelihood coefficients alone. Likewise, fixed mixing changes action frequencies as well as progress conditioning. Section 4.7 and the limitations now make these attribution boundaries explicit.

For clarity, revised curve bands show mean ±1 SEM over ten seeds, with sample SD computed using ddof=1. The seed is the statistical unit, and the paired tests and Holm corrections are reported separately; we do not infer significance from overlap of the bands.

For completeness, the separate archived block-level intervention reports:

Task / configurationEndpointRaw ppTrajectoryRaw pp
Rastrigin: full AMS4528.6-5146.4-
Rastrigin: remove DP guidance7773.10.00208107.10.0020
Rastrigin: fixed information-guided4858.10.08405156.20.2324
Rastrigin: replace full training mechanism4745.30.16025441.70.0840
Rosenbrock: full AMS (millions)1.367-4.565-
Rosenbrock: remove DP guidance20.6510.002032.0710.0020
Rosenbrock: fixed information-guided1.5870.00203.8180.0020
Rosenbrock: replace full training mechanism20.1530.002027.1950.0020

The archived experiment is reported in Section 4.7 and Table 6; the matched controls are in Appendix F.2, Table 10 and Figure 8; the statistical and attribution boundaries are stated in the Limitations section.

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Paper summary

This paper develops a new method for performing Bayesian Optimization in very large problems. The goal is to perform computationally efficiently as the number, n, of observed data points grows; but also to be sure to arrive at or near a maximum of the function with as few function evaluations as possible, especially when those evaluations are expensive, as in the robotics training domain.

The proposed strategy is heterogeneous: a policy first diagnoses what qualitative type of regime the optimization process is currently in, and uses that information to propose particular short-term sampling and search strategies.

Experiments seem to show that this adaptivity is valuable, and interestingly that all the different search strategies seem to have an important role to play.

Critical strengths

The paper made a hard topic clear and addresses an important question.

The experiments were carefully executed and the proposed method seems to yield a real improvement on a variety of problem types.

Critical weaknesses

Fundamentally, this method seems to be kind of ad hoc. I do appreciate that it is pieced together out of formally well-justified components; and that those individual components made assumptions about the domain they were working in. So it does in a way make sense that, to "cover the territory" of optimization problems, we will in fact exactly need to put together multiple strategies.

In the modern world, the competing idea would be to train some sort of very general-purpose sample-selection policy via RL. Would that make sense? It would have to be trained on a very wide variety of problem types to be able to operate effectively, over such a wide range of problems. And it would probably need some careful input-representation design, to capture appropriate statistics (or even more training and a recurrent representation that figures out its own statistics).

Questions for authors
  • I couldn't quite tell what the time-scale of adaptation is here. I think it is all within a single problem. Is that right? What about "meta-learning" across problems?

  • Does the time cost of gathering a new sample enter explicitly into the decision policy? It seems like it should: when samples are cheap to gather we can think less hard about which ones we need,

4 comments

Thank you for recognizing the importance of the problem and the care in the experimental comparisons. Your questions helped us clarify what adapts, what remains fixed, and the scope of the contribution.

Q1. The proposed method appears somewhat ad hoc. Would it instead make sense to train a general-purpose sample-selection policy using reinforcement learning?

A. We agree that the controller is a heuristic integration of search operators. We do not claim an optimal switching policy or that every operator is necessary on every problem. The intended contribution is a concrete mechanism for allocating a sparse-GP BO batch across centers, scales, and local/global actions, supported by comparisons and component interventions.

We have strengthened and qualified the evidence. Removing DP-guided proposals worsens both endpoint and trajectory-averaged regret on both 500-D tasks, with Holm-adjusted (p_H=0.0234) for each comparison in the archived twelve-test family (Table 6). We also completed a fixed four-action mixture and a likelihood-only control, each with ten matched seeds on both tasks (Table 10 and Figure 8). The fixed mixture has worse mean performance than the new full baseline on Rosenbrock, but its raw (p=0.0137) becomes (p_H=0.1094) after the eight-test correction. The Rastrigin mixture comparisons do not establish an advantage, and the likelihood-only intervention also does not yield statistically significant differences. We therefore describe the component evidence as task- and metric-dependent rather than attributing all gains to switching or likelihood weights. The revised limitations state this explicitly.

Training a policy across problems, including with RL, is a reasonable alternative. It would require a task distribution, a state representation, a reward that reflects the desired trade-off, and evaluation on held-out problems. Our method has no such cross-task policy-training stage and does not claim superiority over a learned policy. Its shared constants are fixed design choices, not parameters learned through meta-training.

Regret values below are mean endpoint / trajectory-averaged regret:

ConfigurationRastrigin 500-DRosenbrock 500-D
Full AMS, matched-control protocol4703.1 / 5363.71.374M / 4.567M
Fixed four-action mixture5195.4 / 5810.83.022M / 8.638M
Equal likelihood coefficients4878.2 / 5475.71.371M / 4.567M

For the fixed mixture on Rosenbrock, both raw paired p-values are 0.0137, but both become pH=0.1094p_H=0.1094 in the eight-test family. The corresponding Rastrigin values are 0.1934 and pH=0.7734p_H=0.7734. Equal-likelihood comparisons have raw p-values from 0.1055 to 1 and do not establish a difference.

The separate archived block-removal experiment gives:

TaskArchived full AMSRemove DP guidance
Rastrigin 500-D4528.6 / 5146.47773.1 / 8107.1
Rosenbrock 500-D1.367M / 4.565M20.651M / 32.071M

All four DP-removal comparisons have raw p=0.0020p=0.0020 and Holm-adjusted pH=0.0234p_H=0.0234 in the archived twelve-test family. The archived intervention is reported in Section 4.7 and Table 6, and the matched controls are in Appendix F.2, Table 10 and Figure 8. The Limitations section explicitly notes that the component effects are task- and metric-dependent and that higher-order interactions and broader threshold sensitivity remain open.

Q2. Is the adaptation performed within a single optimization problem, and what is the relationship to meta-learning across problems?

A. Your interpretation is correct. The controller makes one decision per BO batch within a single problem. Its rules and numerical constants are fixed; the quantities supplied to those rules change with the observed history. These include incumbent progress, the previous requested action, the accumulated stagnation count, and the clustering state. The controller and spatial state are initialized afresh for each run. Consequently, a fixed implementation can produce different action sequences as a run evolves. This is the meaning of adaptation in our paper.

Section 3 now makes this time scale explicit and specifies the progress statistic, action priorities, and update order. Appendix A.2 gives the constants, cluster gate, and spatial scales. The same controller constants were used across the eight benchmarks without task-specific controller tuning.

The resulting executed-action shares are:

TaskInformationMulti-scaleContractionEscape
Ackley12.08 +/- 5.71%34.58 +/- 4.41%41.25 +/- 8.44%12.08 +/- 2.37%
Rastrigin17.14 +/- 3.69%39.64 +/- 3.93%32.50 +/- 5.94%10.71 +/- 0.00%
Rosenbrock19.00 +/- 4.98%40.00 +/- 0.00%27.67 +/- 4.98%13.33 +/- 0.00%

These are mean +/- sample SD over ten seeds and count executed controller batches, not wall-clock time. They illustrate how a fixed implementation produces different action sequences as its incumbent history, stagnation count, previous action, and clustering state evolve. The multi-seed action data are reported in Figure 4 and Appendix F.5, Table 14.

Q3. Does the time cost of obtaining a new observation explicitly enter the decision policy, especially when observations are cheap to collect?

A. No. The current decision rule does not use the measured duration or monetary cost of an individual function evaluation. It addresses evaluation efficiency at a fixed evaluation budget, while computational runtime is reported separately. We now state this explicitly in Section 3.

We agree that cheaper observations can favor spending less computation on each decision, and heterogeneous evaluation costs motivate a cost-aware policy. These trade-offs are not resolved by the present controller. Section 4.3 reports full-run computational costs, and Appendix F.7 adds an independent measurement of the clustering refresh overhead. The original runtime summary averages within each task and then weights the eight task means equally; it does not imply equal runtimes across tasks.

These clarifications distinguish the demonstrated within-run adaptation from the broader directions of meta-learning and cost-aware decision making.

The reported computational results are separate wall-clock measurements:

MethodMean task-level wall-clock across eight tasks
Adaptive-depth FocalBO6798 +/- 2578 s
AMS-DVGP2694 +/- 1038 s
SVGP1393 +/- 526 s

An independent single-thread profile measures the full-covariance mixture refresh at 2.804 +/- 0.023 s for (n,d)=(1000,500)(n,d)=(1000,500) and 5.917 +/- 0.545 s for (n,d)=(2000,500)(n,d)=(2000,500), with K=20K=20. The full-run summary is in Section 4.3 and Table 7; the independent refresh profile is in Appendix F.7 and Table 16.

Thanks for the helpful answers to my questions.

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