Reshuffling Resampling Splits Can Improve Generalization of Hyperparameter Optimization

Authors: thomas  nagler
lennart  schneider
bernd  bischl
matthias  feurer
Venue: NeurIPS_cc_2024_Conference
Published: 2024-04-29 19:01:31

Abstract: Hyperparameter optimization is crucial for obtaining peak performance of machine learning models. The standard protocol evaluates various hyperparameter configurations using a resampling estimate of the generalization error to guide optimization and select a final hyperparameter configuration. Without much evidence, paired resampling splits, i.e., either a fixed train-validation split or a fixed cross-validation scheme, are often recommended. We show that, surprisingly, reshuffling the splits for every configuration often improves the final model's generalization performance on unseen data. Our theoretical analysis explains how reshuffling affects the asymptotic behavior of the validation loss surface and provides a bound on the expected regret in the limiting regime. This bound connects the potential benefits of reshuffling to the signal and noise characteristics of the underlying optimization problem. We confirm our theoretical results in a  controlled simulation study and demonstrate the practical usefulness of reshuffling in a large-scale, realistic hyperparameter optimization experiment. While reshuffling leads to test performances that are competitive with using fixed splits, it drastically improves results for a single train-validation holdout protocol and can often make holdout become competitive with standard CV while being computationally cheaper.

Main paper: 
 introduction: 
 Hyperparameters have been shown to strongly influence the performance of machine learning models (van Rijn & Hutter, 2018; Probst et al., 2019) . The primary goal of hyperparameter optimization (HPO; also called tuning) is the identification and selection of a hyperparameter configuration (HPC) that minimizes the estimated generalization error (Feurer & Hutter, 2019; Bischl et al., 2023) . Typically, this task is challenged by the absence of a closed-form mathematical description of the objective function, the unavailability of an analytic gradient, and the large cost to evaluate HPCs, categorizing HPO as a noisy, black-box optimization problem. An HPC is evaluated via resampling, such as a holdout split or M -fold cross-validation (CV), during tuning. These resampling splits are usually constructed in a fixed and instantiated manner, i.e., the same training and validation splits are used for the internal evaluation of all configurations. On the one hand, this is an intuitive approach, as it should facilitate a fair comparison between HPCs and reduce the variance in the comparison. 1 On the other hand, such a fixing of train and validation splits might steer the optimization, especially after a substantial budget of evaluations, towards favoring HPCs which are specifically tailored to the chosen splits. Such and related effects, where we "overoptimize" the validation performance without effective reward in improved generalization performance have been sometimes dubbed "overtuning" or "oversearching". For a more detailed discussion of this topic, including related work, see Section 5 and Appendix B. The practice of reshuffling resampling splits during HPO is generally neither discussed in the scientific literature nor HPO software tools. 2 To the best of our knowledge, only Lévesque (2018) investigated reshuffling train-validation splits for every new HPC. For both holdout and M -fold CV using reshuffled resampling splits resulted in, on average, slightly lower generalization error when used in combination with Bayesian optimization (BO, Garnett, 2023) or CMA-ES (Hansen & Ostermeier, 2001) as HPO algorithms. Additionally, reshuffling was used by a solution to the NeurIPS 2006 performance prediction challenge to estimate the final generalization performance (Guyon et al., 2006) . Recently, in the context of evolutionary optimization, reshuffling was applied after every generation (Larcher & Barbosa, 2022) .In this paper, we systematically examine the effect of reshuffling on HPO performance. Our contributions can be summarized as follows:1. We show theoretically that reshuffling resampling splits during HPO can result in finding a configuration with better overall generalization performance, especially when the loss surface is rather flat and its estimate is noisy (Section 2).2. We confirm these theoretical insights through controlled simulation studies (Section 3).3. We demonstrate in realistic HPO benchmark experiments that reshuffling splits can lead to a real-world improvement of HPO (Section 4). Especially in the case of reshuffled holdout, we find that the final generalization performance is often on par with 5-fold CV under a wide range of settings.We discuss results, limitations, and avenues for future research in Section 5.2 Theoretical Analysis 
problem statement and setup: 
 Machine learning (ML) aims to fit a model to data, so that it generalizes well to new observations of the same distribution. Let D = {Z i } n i=1 be the observed dataset consisting of i.i.d. random variables from a distribution P , i.e., in the supervised setting Z i = (X i , Y i ). 3,4 Formally, an inducer g configured by an HPC λ ∈ Λ maps a dataset D to a model from our hypothesis space h = g λ (D) ∈ H. During HPO, we want to find a HPC that minimizes the expected generalization error, i.e., find λ * = arg min λ∈Λ µ(λ), where µ(λ) = E[ℓ(Z, g λ (D))],where ℓ(Z, h) is the loss of model h on a fresh observation Z. In practice, there is usually a limited computational budget for each HPO run, so we assume that there is only a finite number of distinct HPCs Λ = {λ 1 , . . . , λ J } to be evaluated, which also simplifies the subsequent analysis. Naturally, we cannot optimize the generalization error directly, but only an estimate of it. To do so, a resampling is constructed. For every HPC λ j , draw M random sets I 1,j , . . . , I M,j ⊂ {1, . . . , n} of validation indices with n valid = ⌈αn⌉ instances each. The random index draws are assumed to be independent of the observed data. The data is then split accordingly into pairs V m,j = {Z i } i∈Im,j , T m,j = {Z i } i / ∈Im,j of disjoint validation and training sets. Define the validation loss on the m-th fold and the M -fold validation loss asµ(λ j ) = 1 M M m=1L(V m,j , g λj (T m,j )).Since µ is unknown, we minimize λ = arg min λ∈Λ µ(λ), hoping that µ( λ) will also be small. Typically, the same splits are used for every HPC, so I m,j = I m for all j = 1, . . . , J and m = 1, . . . , M . In the following, we investigate how reshuffling train-validation splits (i.e., I m,j ̸ = I m,j ′ for j ̸ = j ′ ) affects the HPO problem.We first investigate how different validation and reshuffling strategies affect the empirical loss surface µ. In particular, we derive the limiting distribution of the sequence √ n( µ(λ j ) -µ(λ j )) J j=1 . This limiting regime will not only reveal the effect of reshuffling on the loss surface, but also give us a tractable setting to study HPO performance. Theorem 2.1. Under regularity conditions stated in Appendix C.1, it holds √ n ( µ(λ j ) -µ(λ j ))J j=1 → N (0, Σ) in distribution, whereΣ i,j = τ i,j,M K(λ i , λ j ), τ i,j,M = lim n→∞ 1 nM 2 α 2 n s=1 M m=1 M m ′ =1Pr(s ∈ I m,i ∩ I m ′ ,j ), andK(λ i , λ j ) = lim n→∞ Cov[ ln (Z ′ , λ i ), ln (Z ′ , λ j )], ln (z, λ) = E[ℓ(z, g λ (T ))] -E[ℓ(Z, g λ (T ))],where the expectation is taken over a training set T of size n and two fresh samples Z, Z ′ from the same distribution.The regularity conditions are rather mild and discussed further in Appendix C.1. The kernel K reflects the (co-)variability of the losses caused by validation samples. The contribution of training samples only has a higher-order effect. The validation scheme enters the distribution through the quantities τ i,j,M . In what follows, we compute explicit expressions for some popular examples. The following list provides formal definitions for the index sets I m,j .(i) (holdout) Let M = 1 and I 1,j = I 1 for all j = 1, . . . , J, and some size-⌈αn⌉ index set I 1 . (ii) (reshuffled holdout) Let M = 1 and I 1,1 , . . . , I 1,J be independently drawn from the uniform distribution over all size-⌈αn⌉ subsets from {1, . . . , n}. (iii) (M -fold CV) Let α = 1/M and I 1 , . . . , I M be a disjoint partition of {1, . . . , n}, and I m,j = I m for all j = 1, . . . , J.(iv) (reshuffled M -fold CV) Let α = 1/M and (I 1,j , . . . , I M,j ), j = 1, . . . , J, be independently drawn from the uniform distribution over disjoint partitions of {1, . . . , n}. (v) (M -fold holdout) Let I m , m = 1, . . . , M , be independently drawn from the uniform distribution over size-⌈αn⌉ subsets of {1, . . . , n} and set I m,j = I m for all m = 1, . . . , M, j = 1, . . . , J. (vi) (reshuffled M -fold holdout) Let I m,j , m = 1, . . . , M, j = 1, . . . , J, be independently drawn from the uniform distribution over size-⌈αn⌉ subsets of {1, . . . , n}.The value of τ i,j,M for each example is computed explicitly in Appendix E. In all these examples, we in fact haveEQUATIONfor some method-dependent parameters σ, τ shown in Table 1 . The parameter σ 2 captures any increase in variance caused by omitting an observation from the validation sets. The parameter τ quantifies a potential decrease in correlation in the loss surface due to reshuffling. More precisely, holdout (HO) 1/α 1 reshuffled HO 1/α α M -fold CV 1 1 reshuffled M -fold CV 1 1 M -fold HO (subsampling / Monte Carlo CV) 1 + (1 -α)/M α 1 reshuffled M -fold HO 1 + (1 -α)/M α 1/(1 + (1 -α)/M α)the observed losses µ(λ i ), µ(λ j ) at distinct HPCs λ i ̸ = λ j become less correlated when τ is small. Generally, an increase in variance leads to worse generalization performance. The effect of a correlation decrease is less obvious and is studied in detail in the following section.We make the following observations about the differences between methods in Table 1 :• M -fold CV incurs no increase in variance (σ 2 = 1) and -because every HPC uses the same folds -no decrease in correlation. Interestingly, the correlation does not even decrease when reshuffling the folds. In any case, all samples are used exactly once as validation and training instance. At least asymptotically, this leads to the same behavior, and reshuffling should have almost no effect on M -fold CV.• The two (1-fold) holdout methods bear the same 1/α increase in variance. This is caused by only using a fraction α of the data as validation samples. Reshuffled holdout also decreases the correlation parameter τ 2 . In fact, if HPCs λ i ̸ = λ j are evaluated on largely distinct samples, the validation losses µ(λ i ) and µ(λ j ) become almost independent.• M -fold holdout also increases the variance, because some samples may still be omitted from validation sets. This increase is much smaller for large M . Accordingly, the correlation is also decreased by less in the reshuffled variant.In practice, we are mainly interested in the performance of a model trained with the optimal HPC λ.To simplify the analysis, we explore this in the large-sample regime derived in the previous section. AssumeEQUATIONwhere ϵ(λ) is a zero-mean Gaussian process with covariance kernel Cov(ϵ(λ), ϵ(λ ′ )) = K(λ, λ) if λ = λ ′ , τ 2 K(λ, λ ′ ) else. (3) Let Λ ⊆ {λ ∈ R d : ∥λ∥ ≤ 1} with |Λ| = J < ∞κ = sup ∥λ∥,∥λ ′ ∥≤1 |K(λ, λ) -K(λ, λ ′ )| K(λ, λ)∥λ -λ ′ ∥ 2 .can be interpreted as a measure of correlation of the process ϵ. In particular,Corr(ϵ(λ), ϵ(λ ′ )) ≥ 1 -κ∥λ -λ ′ ∥ 2 .The constant is small when ϵ is strongly correlated, and large otherwise. Further, define η as the minimal number such that any η-ball contained in {∥λ∥ ≤ 1} contains at least one element of Λ. It measures how densely the set of candidate HPCs Λ covers set of all possible HPCs. If Λ is a deterministic uniform grid, we have about η ≈ J -1/d . Similarly, Lemma D.1 in the Appendix shows that η ≲ J -1/2d when randomly sampling HPCs. Finally, the constant measures the local curvature at the minimum of the loss surface µ. Finding an HPC λ close to the theoretical optimum λ * is easier when the minimum is more pronounced (large m). On the other hand, the regret µ(λ) -µ(λ * ) is also punishing mistakes more quickly. Defining log(x) + = max{0, log(x)}, we can now state our main result. Theorem 2.2. Let µ follow the Gaussian process modelm = sup λ∈Λ |µ(λ) -µ(λ * )| ∥λ -λ * ∥ 2 ,(2). Suppose κ < ∞, 0 < σ 2 ≤ Var[ϵ(λ)] ≤ σ 2 < ∞ for all λ ∈ Λ, and m > 0. Then E[µ( λ) -µ(λ * )] ≤ σ √ d[8 + B(τ ) -A(τ )].whereB(τ ) = 48 1 -τ 2 log J + τ 1 + log(3κ) + , A(τ ) = 1 -τ 2 (σ/σ) log σ 2mη 2 + .The numeric constants result from several simplifications in a worst-case analysis, which lowers their practical relevance. A qualitative analysis of the bound is still insightful. The bound is increasing in σ and d, indicating that the HPO problem is harder when there is a lot of noise or there are many parameters to tune. The terms B(τ ) and A(τ ) have conceptual interpretations:• The term B(τ ) quantifies how likely it is to pick a bad λ because of bad luck: a λ far away from λ * had such a small ϵ(λ) that it outweighs the increase in µ. Such events are more likely when the process ϵ is weakly correlated. Accordingly, B(τ ) is decreasing in τ and increasing in κ.• The term A(τ ) quantifies how likely it is to pick a good λ by luck: a λ close to λ * had such a small ϵ(λ) that it overshoots all the other fluctuations. Also such events are more likely when the process ϵ is weakly correlated. Accordingly, the term A(τ ) is decreasing in τ .The B, as stated, is unbounded, but a closer inspection of the proof shows that it is upper bounded by √ log J. This bound is attained only in the unrealistic scenario when the validation losses are essentially uncorrelated across all HPCs. The term A is bounded from below by zero, which is also the worst case because the term enters our regret bound with a negative sign.Both A and B are decreasing in the reshuffling parameter τ . There are two regimes. If σ/2mη 2 ≤ e, then A(τ ) = 0 and reshuffling cannot lead to an improvement of the bound. The term σ/mη 2 can be interpreted as noise-to-signal ratio (relative to the grid density). If the signal is much stronger than the noise, the HPO problem is so easy that reshuffling will not help. This situation is illustrated in Figure 1a .If on the other hand σ/mη 2 > e, the terms A(τ ) and B(τ ) enter the bound with opposing signs. This creates tension: reshuffling between HPCs increases B(τ ), which is countered by a decrease in A(τ ). So which scenarios favor reshuffling? When the process ϵ is strongly correlated, κ is small and reshuffling (decreasing τ ) incurs a high cost in B(τ ). This is intuitive: When there is strong correlation, the validation loss surface µ is essentially just a vertical shift of µ. Finding the optimal λ is then almost as easy as if we would know µ, and decorrelating the surface through reshuffling would make it unnecessarily hard. When ϵ is less correlated (κ large) however, reshuffling does not hurt the term B(τ ) as much, but we can reap all the benefits of increasing A(τ ). Here, the effect of reshuffling can be interpreted as hedging against the catastrophic case where all µ(λ) close to the optimal λ * are simultaneously dominated by a region of bad hyperparameters. This is illustrated in Figure 1b .Question: Does the paper discuss the limitations of the work performed by the authors?Answer: [Yes] Justification: The paper provides an analysis of reshuffling data in the context of estimating the generalization error for hyperparameter optimization. Our theoretical analysis explains why reshuffling works, and we experimentally verify the theoretical analysis. We discuss the limitations of our work in Section 5.Guidelines:• The answer NA means that the paper has no limitation while the answer No means that the paper has limitations, but those are not discussed in the paper. • The authors are encouraged to create a separate "Limitations" section in their paper.• The paper should point out any strong assumptions and how robust the results are to violations of these assumptions (e.g., independence assumptions, noiseless settings, model well-specification, asymptotic approximations only holding locally). The authors should reflect on how these assumptions might be violated in practice and what the implications would be. • The authors should reflect on the scope of the claims made, e.g., if the approach was only tested on a few datasets or with a few runs. 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simulation study: 
 To test our theoretical understanding of the potential benefits of reshuffling resampling splits during HPO, we conduct a simulation study. This study helps us explore the effects of reshuffling in a controlled setting.We construct a univariate quadratic loss surface function µ : Λ ⊂ R → R, λ → m(λ -0.5) 2 /2 which we want to minimize. The global minimum is given at µ(0.5) = 0. Combined with a kernel for the noise process ϵ as in Equation ( 3), this allows us to simulate an objective as observed during HPO by sampling µ(λ) = µ(λ) + ϵ(λ). We use a squared exponential kernelK(λ, λ ′ ) = σ 2 K exp (-κ(λ -λ ′ ) 2 /2) that is plugged into the covariance kernel of the noise process ϵ in Equation ( 3). The parameters m and κ in our simulation setup correspond exactly to the curvature and correlation constants from the previous sections. Recall that Theorem 2.2 states that the effect of reshuffling strongly depends on the curvature m of the loss surface µ (a larger m implies a stronger curvature) and the constant κ as a measure of correlation of the noise ϵ (a larger κ implies weaker correlation). Combined with the possibility to vary τ in the covariance kernel of ϵ, we can systematically investigate how curvature of the loss surface, correlation of the noise and the extent of reshuffling affect optimization performance. In each simulation run, we simulate the observed objective μ(λ), identify the minimizer λ = arg min λ∈Λ μ(λ), and calculate its true risk, µ( λ). We repeat this process 10000 times for various combinations of τ , m, and κ.Figure 2 visualizes the true risk of the configuration λ that minimizes the observed objective. We observe that for a loss surface with low curvature (i.e., m ≤ 2), reshuffling is beneficial (lower values of τ resulting in a better true risk of the configuration that optimizes the observed objective) as long as the noise process is not too correlated (i.e., κ ≥ 1). As soon as the noise process is more strongly correlated, even flat valleys of the true risk µ remain clearly visible in the observed risk µ, and reshuffling starts to hurt the optimization performance. Moving to scenarios of high curvature, the general relationship of m and κ remains the same, but reshuffling starts to hurt optimization performance already with weaker correlation in the noise. In summary, the simulations show that in cases of low curvature of the loss surface, reshuffling (reducing τ ) tends to improve the true risk of the optimized configuration, especially when the loss surface is flat (small m) and the noise is not strongly correlated (i.e., κ is large). This exactly confirms our theoretical predictions from the previous section.Justification: We report the standard error in every analysis.Guidelines:• The answer NA means that the paper does not include experiments.• The authors should answer "Yes" if the results are accompanied by error bars, confidence intervals, or statistical significance tests, at least for the experiments that support the main claims of the paper. • The factors of variability that the error bars are capturing should be clearly stated (for example, train/test split, initialization, random drawing of some parameter, or overall run with given experimental conditions). • The method for calculating the error bars should be explained (closed form formula, call to a library function, bootstrap, etc.) • The assumptions made should be given (e.g., Normally distributed errors).• It should be clear whether the error bar is the standard deviation or the standard error of the mean. • It is OK to report 1-sigma error bars, but one should state it. The authors should preferably report a 2-sigma error bar than state that they have a 96% CI, if the hypothesis of Normality of errors is not verified. • For asymmetric distributions, the authors should be careful not to show in tables or figures symmetric error bars that would yield results that are out of range (e.g. negative error rates). • If error bars are reported in tables or plots, The authors should explain in the text how they were calculated and reference the corresponding figures or tables in the text. 
benchmark experiments: 
 In this section, we present benchmark experiments of real-world HPO problems where we investigate the effect of reshuffling resampling splits during HPO. First, we discuss the experimental setup. Second, we present results for HPO using random search (Bergstra & Bengio, 2012) . Third, we also show the effect of reshuffling when applied in BO using HEBO (Cowen-Rivers et al., 2022) and SMAC3 (Lindauer et al., 2022) . Recall that our theoretical insight suggests that 1) reshuffling might be beneficial during HPO and 2) holdout should be affected the most by reshuffling and other resamplings should only be affected to a lesser extent. Figure 2 : Mean true risk (lower is better) of the configuration minimizing the observed objective systematically varied with respect to curvature m, correlation strength κ of the noise (a larger κ implying weaker correlation), and extent of reshuffling τ (lower τ increasing reshuffling). A τ of 1 indicates no reshuffling. Error bars represent standard errors.As benchmark tasks, we use a set of standard HPO problems defined on small-to medium-sized tabular datasets for binary classification. We suspect the effect of the resampling variant used and whether the resampling is reshuffled to be larger for smaller datasets, where the variance of the validation loss estimator is naturally higher. Furthermore, from a practical perspective, this also ensures computational feasibility given the large number of HPO runs in our experiments. We systematically vary the learning algorithm, optimized performance metric, resampling method, whether the resampling is reshuffled, and the size of the dataset used for training and validation during HPO. Below, we outline the general experimental design and refer to Appendix F for details.We used a subset of the datasets defined by the AutoML benchmark (Gijsbers et al., 2024) , treating these as data generating processes (DGPs; Hothorn et al., 2005) . We only considered datasets with less than 100 features to reduce the required computation time and required the number of observations to be between 10000 and 1000000; for further details see Appendix F.1. Our aim was to robustly measure the generalization performance when varying the size n, which, as defined in Section 2 denotes the size of the combined data for model selection, so one training and validation set combined. First, we sampled 5000 data points per dataset for robust assessment of the generalization error; these points are not used during HPO in any way. Then, from the remaining points we sampled tasks with n ∈ {500, 1000, 5000}.We selected CatBoost (Prokhorenkova et al., 2018) and XGBoost (Chen & Guestrin, 2016) for their state-of-the-art performance on tabular data (Grinsztajn et al., 2022; Borisov et al., 2022; McElfresh et al., 2023; Kohli et al., 2024) . Additionally, we included an Elastic Net (Zou & Hastie, 2005) to represent a linear baseline with a smaller search space and a funnel-shaped MLP (Zimmer et al., 2021) as a cost-effective neural network baseline. We provide details regarding training pipelines and search spaces in Appendix F.2.We conduct a random search with 500 HPC evaluations for every resampling strategy we described in We also investigated the effect of reshuffling on two state-of-the-art BO variants (Eggensperger et al., 2021; Turner et al., 2021) , namely HEBO (Cowen-Rivers et al., 2022) and SMAC3 (Lindauer et al., 2022) . The experimental design was the same as for random search, except for the budget, which we reduced from 500 HPCs to 250 HPCs, and only optimized ROC AUC.In the following, we focus on the results obtained using ROC AUC. We present aggregated results over different tasks, learning algorithms and replications to get a general understanding of the effects. Unaggregated results and results involving accuracy and logloss can be found in Appendix G.For each resampling (holdout, 5-fold holdout, 5-fold CV, and 5x 5-fold CV), we empirically analyze the effect of reshuffling train and validation splits during HPO.In Figure 3 we exemplarily show how test performance develops over the course of an HPO run on a single task for different resamplings (with and without reshuffling). Naturally, test performance does not necessarily increase in a monotonic fashion, and especially holdout without reshuffling tends to be unstable. Its reshuffled version results in substantially better test performance.Next, we look at the relative improvement (compared to standard 5-fold CV, which we consider our baseline) with respect to test ROC AUC performance of the incumbent over time in Figure 4 , i.e., the difference in test performance of the incumbent between standard 5-fold CV and a different resampling protocol; hence a positive difference tells us how much better in test error we are, if we would have chosen the other protocol instead 5-fold CV. We observe that reshuffling generally results in equal or better performance compared to the same resampling protocol without reshuffling.For 5-fold holdout and especially 5-fold CV and 5x 5-fold CV, reshuffling has a smaller effect on relative test performance improvement, as expected. Holdout is affected the most by reshuffling and results in substantially better relative test performance compared to standard holdout. We also observe that an HPO protocol based on reshuffled holdout results in similar final test performance as standard 5-fold CV while overall being substantially cheaper due to requiring less model fits per HPC evaluation. In Appendix G.2, we further provide an ablation study on the number of folds when using M -fold holdout, where we observed that -in line with our theory -the more folds are used, the less reshuffling affects M -fold holdout. However, this general trend can vary for certain combinations of classifier and performance metric, see Appendix G. Especially for logloss, we observed that reshuffling rarely is beneficial; see the discussion in Section 5. Finally, the different resamplings generally behave as expected. The more we are willing to invest compute resources into a more intensive resampling like 5-fold CV or 5x 5-fold CV, the better the generalization performance of the final incumbent.Results for BO and Reshuffling Figure 5 shows that, generally HEBO and SMAC3 outperform random search with respect to generalization performance (i.e., comparing HEBO and SMAC3 to random search under standard holdout, or comparing under reshuffled holdout). More interestingly, HEBO, SMAC3 and random search all strongly benefit from reshuffling. Moreover, the performance gap between HEBO and random search but also SMAC3 and random search narrows when the resampling is reshuffled, which is an interesting finding of its own: As soon as we are concerned with generalization performance of HPO and not only investigate validation performance during optimization, the choice of optimizer might have less impact on final generalization performance compared to other choices such as whether the resampling is reshuffled during HPO or not. We present results for BO and reshuffling for different resamplings in Appendix G.  
discussion: 
 In the previous sections, we have shown theoretically and empirically that reshuffling can enhance generalization performance of HPO. The main purpose of this article is to draw attention to this surprising fact about a technique that is simple but rarely discussed. Our work goes beyond a preliminary experimental study on reshuffling (Lévesque, 2018) , in that we also study the effect of reshuffling on random search, multiple metrics and learning algorithms, and most importantly, for the first time, we provide a theoretical analysis that explains why reshuffling can be beneficial.Limitations To unveil the mechanisms underlying the reshuffling procedures, our theoretical analysis relies on an asymptotic approximation of the empirical loss surface. This allows us to operate on Gaussian loss surfaces, which exhibit convenient concentration and anti-concentration properties required in our proof. The latter are lacking for general distributions, which explains our asymptotic approach. The analysis was further facilitated by a loss stability assumption regarding the learning algorithms that is generally rather mild; see the discussion in Bayle et al. (2020) . However, it typically fails for highly sensitive losses, which has practical consequences. In fact, Figure 9 in Appendix G shows that reshuffling usually hurts generalization for the logloss and small sample sizes. It is still an open question whether this problem can be fixed by less naive implementations of the technique.Another limitation is our focus on generalization after search through a fixed, finite set of candidates. This largely ignores the dynamic nature of many HPO algorithms, which would greatly complicate our analysis. Finally, our experiments are limited in that we restricted ourselves to tabular data and binary classification and we avoided extremely small or large datasets.The fact that generalization performance can decrease during HPO (or computational model selection in general) is sometimes known as oversearching, overtuning, or overfitting to the validation set (Quinlan & Cameron-Jones, 1995; Escalante et al., 2009; Koch et al., 2010; Igel, 2012; Bischl et al., 2023 ), but has arguably not been studied very thoroughly. Given recent theoretical (Feldman et al., 2019) and empirical (Purucker & Beel, 2023 ) findings, we expect less overtuning on multi-class datasets, making it interesting to see how reshuffling would affect the generalization performance.Several works suggest strategies to counteract this effect. First, LOOCVCV proposes a conservative choice of incumbents (Ng, 1997) at the cost of leave-one-out analysis or an additional hyperparameter. Second, it is possible to use an extra selection set (Igel, 2012; Lévesque, 2018; Mohr et al., 2018) at the cost of reduced training data, which was found to lead to reduced overall performance (Lévesque, 2018) . Third, by using early stopping one can stop hyperparameter optimization before the generalization performance degrades again. This was so far demonstrated to be able to save compute budget at only marginally reduced performance, but also requires either a sensitivity hyperparameter or correct estimation of the variance of the generalization estimate and was only developed for cross-validation so far (Makarova et al., 2022) . Reshuffling itself is orthogonal to these proposals and a combination with the above-mentioned methods might result in further improvements.Outlook Generally, the related literature detects overfitting to the validation set either visually (Ng, 1997) or by measuring it (Koch et al., 2010; Igel, 2012; Fabris & Freitas, 2019) . Developing a unified formal definition of the above-mentioned terms and thoroughly analyzing the effect of decreased generalization performance after many HPO iterations and how it relates to our measurements of the validation performance is an important direction for future work.We further found, both theoretically and experimentally, that investing more resources when evaluating each HPC can result in better final HPO performance. To reduce the computational burden on HPO again, we suggest further investigating the use of adaptive CV techniques, as proposed by Auto-WEKA (Thornton et al., 2013) or under the name Lazy Paired Hyperparameter Tuning (Zheng & Bilenko, 2013) . Designing more advanced HPO algorithms exploiting the reshuffling effect should be a promising avenue for further research. Due to the black box nature of the HPO problem (Feurer & Hutter, 2019; Bischl et al., 2023) , gradient free, zeroth-order optimization algorithms such as BO (Garnett, 2023) , Evolutionary Strategies (Loshchilov & Hutter, 2016) or a simple random search (Bergstra & Bengio, 2012) have become standard optimization algorithms to tackle vanilla HPO problems.In the last decade, most research on HPO has been concerned with constructing new algorithms that excel at finding configurations with a low estimated generalization error. Examples include BO variants such as as HEBO (Cowen-Rivers et al., 2022) or SMAC3 (Lindauer et al., 2022) . Another direction of HPO research has been concerned with speeding up the HPO process to allow more efficient spending of compute resources. Multifidelity HPO, for example, turns the black box optimization problem into a gray box one by making use of lower fidelity approximations to the target function, i.e., using fewer numbers of epochs or subsets of the data for cheap low-fidelity evaluations that approximate the costly high-fidelity evaluation. Examples include bandit-based budget allocation algorithms such as Successive Halving (Jamieson & Talwalkar, 2016) , Hyperband (Li et al., 2018) and their extensions that use non-random search mechanisms (Falkner et al., 2018; Awad et al., 2021; Mallik et al., 2023) or algorithms making use of multi-fidelity information in the context of BO (Swersky et al., 2014; Klein et al., 2017; Wu et al., 2020; Kadra et al., 2023) . Several works address the problem of speeding up cross-validation techniques and use techniques that could be described as grey box optimization techniques. Besides the ones mentioned in the main paper (Thornton et al., 2013; Zheng & Bilenko, 2013) , it is possible to employ racing techniques for model selection in machine learning as demonstrated by Lang et al. (2015) , and there has been a recent interest in methods that adapt the cost of running full cross-validation procedures (Bergman et al., 2024; Buczak et al., 2024) .When addressing the problem of HPO, we must acknowledge an inherent mismatch between the explicit objective we optimize -namely, the estimated generalization performance of a modeland the actual implicit optimization goal, which is to identify a configuration that yields the best generalization performance on new, unseen data. Typically, evaluations and comparisons of different HPO algorithms focus exclusively on the final best validation performance (i.e., the objective that is directly optimized), even though an unbiased estimate of performance on an external unseen test set might be available. While this approach is logical for assessing the efficacy of an optimization algorithm based on the metric it seeks to improve, relying solely on finding an optimal validation configuration is beneficial only if there is reason to assume a strong correlation between the optimized validation performance and true generalization ability on new, unseen test data. This discrepancy can be found deeply within the HPO community, where the evaluation of HPO algorithms on standard benchmark libraries is usually done solely with respect to the validation performance (Eggensperger et al., 2021; Pineda Arango et al., 2021; Salinas et al., 2022; Pfisterer et al., 2022). 5 This relationship between validation performance (i.e., the estimated generalization error derived from resampling) and true generalization performance (e.g., assessed through an outer holdout test set or additional resampling) of an optimal validation configuration found during HPO remains a largely unexplored area of research.In general, little research has focused on the selection of resampling types, let alone the automated selection of resampling types (Guyon et al., 2010; Feurer et al., 2022) . While we usually expect that a more intensive resampling will reduce the variance of the estimated generalization error and thereby improve the (rank) correlation between optimized validation and unbiased outer test performance within HPCs, this benefit is naturally offset by a higher computational expense. Overall, there is little research on which resampling method to use in practice for model selection, and we only know of a study for support vector machines (Wainer & Cawley, 2017) , a simulation study for clinical prediction models (Dunias et al., 2024) , a study on feature selection (Molinaro et al., 2005) and a study on fast CV (Bergman et al., 2024) . In addition, ML-Plan (Mohr et al., 2018) proposed a two-stage procedure. In a first stage (search), the tool uses planning on hierarchical task networks to find promising machine learning pipelines on 70% of the training data. In a second step (selection), it uses 100% of the training data and retrains the most promising candidates from the search step. Finally, it uses a combination of the internal generalization error estimation that was used during search and the 0.75 percentile of the generalization error estimation from the selection step to make a more unbiased selection of the final model. The paper found that this improves performance over using only regular cross-validation for search and selection. The general consensus, that is in agreement with our findings, is that CV or repeated CV generally leads to better generalization performance. In addition, while there are theoretical works that compare the accuracy of estimating the generalization error of holdout and CV (Blum et al., 1999) , our goals is to correctly identify a single solution, which generalizes well, see the excellent survey by Arlot & Celisse (2010) for a discussion on this topic. Bouthillier et al. (2021) studied the sources of variance in machine learning experiments, and find that the split into training and test data has the largest impact. Consequently, they suggest to reshuffle the data prior to splitting it into the training, which is then used for HPO, and the test set. We followed their suggestion when designing our experiments and draw a new test sample for every replication, see Section 4.1 and Appendix F. This dependence on the exact split was further already discussed in the context of how much the outcome of a statistical test on results of machine learning experiments depended on the exact train-test split (Bouckaert, 2004) .Finally, the first warning against comparing too many hypothesis using cross-validation was raised by Schaffer (1993) , and in addition to the works discussed in Section 5 in the main paper, also picked up by Rao et al. (2008) ; Cawley & Talbot (2010) . Moreover, the problem of finding a correct "upper objective" in a bilevel optimization problem has been noted (Guyon et al., 2010 (Guyon et al., , 2015 (Guyon et al., , 2019)) . Also, in the related field of algorithm configuration the problem has been identified (Eggensperger et al., 2019) .In Table 3 , we provide a brief summary of how resampling is handled in popular HPO libraries and software. 6 For each library, we checked whether the core functionality, examples, or tutorials mention the possibility of reshuffling the resampling during HPO or if the resampling is considered fixed. If reshuffling is used in an example, mentioned, or if core functionality uses it, we mark it with a ✓. If it is unclear or inconsistent across examples and core functionality, we mark it with a ?. Otherwise, we use a ✗. Our conclusion is that the concept of reshuffling resampling generally receives little attention. C.1 Proof of Theorem 2.1We impose stability assumptions on the learning algorithm similar to Bayle et al. (2020) ; Austern & Zhou (2020) . Let Z, Z 1 , . . . , Z n , Z ′ 1 , be iid random variables. Define T = {Z i } n i=1 , and T ′ as T but with Z n replaced by the independent copyZ ′ n . Define ℓ n (z, λ) = ℓ(z, g λ (T )) -E[ℓ(Z, g λ (T )) | T ],assume that each g λ (T ) is invariant to the ordering in T , ℓ is bounded, andEQUATIONThis loss stability assumption is rather mild, see Bayle et al. (2020) for an extensive discussion. Further, define the risk R(g) = E[ℓ(Z, g)] and assume that for every λ ∈ Λ, there is a prediction rule g * λ such thatEQUATIONThis assumption requires g λ (T ) to converge to some fixed prediction rule sufficiently fast and serves as a reasonable working condition for our purposes. It is satisfied, for example, when ℓ is the square loss and g λ is an empirical risk minimizer over a hypothesis class G λ with finite VC-dimension.For further examples, see, e.g., Bousquet & Zhivotovskiy (2021 ), van Erven et al. (2015) , and references therein. The assumption could be relaxed, but this would lead to a more complicated limiting distribution but with the same essential interpretation.Theorem C.1. Under assumptions (4) and (5), it holds√ n ( µ(λ j ) -µ(λ j )) J j=1 → d N (0, Σ), where Σ j,j ′ = τ i,j,M lim n→∞ Cov[ ln (Z, λ j ), ln (Z, λ j ′ )], τ j,j ′ ,M = lim n→∞ 1 nM 2 α 2 n i=1 M m=1 M m ′ =1 Pr(i ∈ I m,j ∩ I m ′ ,j ′ ). Proof. Define µ(λ j ) = 1 M M m=1 E[L(V m,j , g λj (T m,j )) | T m,j ].By the triangle inequality (first and second step), Jensen's inequality (third step), and (5) (last step),E[| µ(λ j ) -µ(λ j )|] ≤ max 1≤m≤M E E[L(V m,j , g λj (T m,j )) | T m,j ] -E[L(V m,j , g λj (T m,j ))] ≤ max 1≤m≤M E E[L(V m,j , g λj (T m,j )) | T m,j ] -E[L(V m,j , g * λj )] + max 1≤m≤M E E[L(V m,j , g λj (T m,j ))] -E[L(V m,j , g * λj )] ≤ 2 max 1≤m≤M E E[L(V m,j , g λj (T m,j )) | T m,j ] -E[L(V m,j , g * λj )] = 2 max 1≤m≤M E R(g λj (T m,j )) -R(g * λj ) = o(1/ √ n).Next, assumption (4) together with Theorem 2 and Proposition 3 of Bayle et al. (2020) yieldEQUATIONi,n ) n i=1 is a triangular array of independent, centered, and bounded random vectors. Because 1(Z i ∈ V m,j ) and Z i are independent, it holds Cov(ξ(j) i,n , ξ (j ′ ) i,n ) = M m=1 M m ′ =1 E[1(i ∈ I m,j ∩ I m ′ ,j ′ )]E[ ln (Z i , λ j ) ln (Z i , λ j ′ )], so lim n→∞ Cov 1 M α √ n n i=1 ξ (j) i,n , 1 M α √ n n i=1 ξ (j ′ ) i,n = lim n→∞ 1 nM 2 α 2 n i=1 Cov ξ (j) i,n , ξ (j ′ ) i,n = Σ j,j ′ .Now the result follows from Lindeberg's central limit theorem for triangular arrays (e.g., van der Vaart, 2000, Proposition 2.27).We want to bound the probability that µ( λ) -µ(λ * ) is large. For some δ > 0, define the set of 'good' hyperparametersΛ δ = {λ j : µ(λ j ) -µ(λ * ) ≤ δ}. Now Pr µ( λ) -µ(λ * ) > δ = Pr λ / ∈ Λ δ = Pr min λ / ∈Λ δ µ(λ) < min λ∈Λ δ µ(λ) ≤ Pr min λ / ∈Λ δ µ(λ) < min λ∈Λ δ/2 µ(λ) = Pr min λ / ∈Λ δ µ(λ) + ϵ(λ) < min λ∈Λ δ/2 µ(λ) + ϵ(λ) ≤ Pr δ + min λ / ∈Λ δ ϵ(λ) < δ/2 + min λ∈Λ δ/2 ϵ(λ) = Pr min λ / ∈Λ δ ϵ(λ) -min λ∈Λ δ/2 ϵ(λ) < -δ/2 = Pr max λ / ∈Λ δ ϵ(λ) -max λ∈Λ δ/2 ϵ(λ) > δ/2 . (ϵ d = -ϵ)There is a tension between the two maxima. The more λ's there are in Λ δ/2 and the less they are correlated, the more likely it is to find one ϵ(λ) that is large. This makes the probability small. However, the less ϵ is correlated, the larger is max λ / ∈Λ δ ϵ(λ), making the probability large. To formalize this, use the Gaussian concentration inequality (Talagrand, 2005, Lemma 2.1.3) :Pr max λ / ∈Λ δ ϵ(λ) -max λ∈Λ δ/2 ϵ(λ) > δ/2 ≤ Pr 2 max λ∈Λ ϵ(λ) -E max λ∈Λ ϵ(λ) > δ/2 -E max λ∈Λ δ/2 ϵ(λ) + E max λ / ∈Λ δ ϵ(λ) ≤ 2 exp - δ/2 -E max λ∈Λ δ/2 ϵ(λ) + E [max λ / ∈Λ δ ϵ(λ)] 2 8σ 2 , provided δ/2-E max λ∈Λ δ/2 ϵ(λ) +E [max λ / ∈Λ δ ϵ(λ)] ≥ 0.We bound the two maxima separately.Recall the definition of m right before Theorem 2.2 and observeΛ δ/2 = {λ : µ(λ) -µ(λ * ) ≤ δ/2} ⊃ {λ : m∥λ -λ * ∥ 2 ≤ δ/2} = {λ : ∥λ -λ * ∥ ≤ (δ/2m) 1/2 } = B(λ * , (δ/2m) 1/2 ).Pack the ball B(λ * , (δ/2m) 1/2 ) with smaller balls with radius η. We can always construct such a packing with at least (δ/2mη 2 ) d/2 elements. By assumption, each small ball contains at least one element of Λ. Pick one element from each small ball and collect them into the setΛ ′ δ/2 . By construction, |Λ ′ δ/2 | ≥ (δ/2mη 2 ) d/2and minλ̸ =λ ′ ∈Λ ′ δ/2 | ∥λ -λ ′ ∥ ≥ η.Sudakov's minoration principle (e.g., Wainwright, 2019, Theorem 5.30) givesE max λ∈Λ δ/2 ϵ(λ) ≥ 1 2 log |Λ ′ δ/2 | min {λ̸ =λ ′ }∩Λ ′ δ/2 Var [ϵ(λ) -ϵ(λ ′ )] ≥ 1 2 log |Λ ′ δ/2 | min ∥λ-λ ′ ∥≥η Var [ϵ(λ) -ϵ(λ ′ )].In general,Var [ϵ(λ) -ϵ(λ ′ )] = K(λ, λ) + K(λ ′ , λ ′ ) -2τ 2 K(λ, λ ′ ) = (1 -τ 2 )[K(λ, λ) + K(λ ′ , λ ′ )] + τ 2 [K(λ, λ) -K(λ, λ ′ )] + τ 2 [K(λ ′ , λ ′ ) -K(λ, λ ′ )] ≥ 2σ 2 (1 -τ 2 ).Hence, we havemin ∥λ-λ ′ ∥≥η Var [ϵ(λ) -ϵ(λ ′ )] ≥ 2σ 2 (1 -τ 2 ),which implies E max λ∈Λ δ/2 ϵ(λ) ≥ 1 2 σ √ d 1 -τ 2 log(δ/2mη 2 ) =: σ √ dA(τ,Var [ϵ(λ) -ϵ(λ k )] ≤ s. Note that sup λ,λ ′ ∈Λ Var [ϵ(λ) -ϵ(λ ′ )] ≤ 2σ, so N (s) = 1 for all s ≥ 2σ. For s 2 ≤ 4σ 2 (1 -τ 2 ), we can use the trivial bound N (s) ≤ J.For s 2 > 4σ 2 (1 -τ 2 ), cover Λ with ℓ 2 -balls of size (s/2στ κ). We can do this with less than N (s) ≤ (6σκ/s) d ∨ 1 such balls. Let λ 1 , . . . , λ N be the centers of these balls. In general, it holdsVar [ϵ(λ) -ϵ(λ ′ )] = K(λ, λ) + K(λ ′ , λ ′ ) -2τ 2 K(λ, λ ′ ) = (1 -τ 2 )[K(λ, λ) + K(λ ′ , λ ′ )] + τ 2 [K(λ, λ) -K(λ, λ ′ )] + τ 2 [K(λ ′ , λ ′ ) -K(λ, λ ′ )] ≤ 2(1 -τ 2 )σ 2 + 2τ 2 σ 2 κ 2 ∥λ -λ ′ ∥ 2 .For s 2 > 4σ 2 (1 -τ 2 ), we thus havesup λ∈Λ min 1≤k≤N (s) Var [ϵ(λ) -ϵ(λ k )] ≤ sup ∥λ-λ ′ ∥2≤(s/2τ σκ) 2 Var [ϵ(λ) -ϵ(λ ′ )] ≤ 2(1 -τ 2 )σ 2 + 2τ 2 σ 2 κ 2 (s/2τ σκ) 2 ≤ s 2 , as desired. Now decompose the integral ∞ 0 log N (s)ds = 2σ √ 1-τ 2 0 log N (s)ds + 2σ 2σ √ 1-τ 2 log N (s)ds ≤ 2σ √ d 1 -τ 2 log J + 2σ 2σ √ 1-τ 2 log N (s)ds.For the second term, compute2σ σ √ 1-τ 2 log N (s)ds ≤ √ d 2σ 2σ √ 1-τ 2 log(6σκ/s) + ds = σ √ d 2 2 √ 1-τ 2 log(6κ/s) + ds ≤ σ √ d 2 0 log(6κ/s) + ds 1/2 2(1 -1 -τ 2 ) 1/2 = σ √ d 2 + 2 log(3κ) + 2(1 -1 -τ 2 ) 1/2 = 2σ √ d 1 + log(3κ) + τ (1 + √ 1 -τ 2 ) 1/2 ≤ 2σ √ dτ 1 + log(3κ) + .We have shown thatE max λ / ∈Λ δ ϵ(λ) ≤ 24σ √ d 1 -τ 2 log J + τ 1 + log(3κ) + =: σ √ dB(τ )/4.Summarizing the two previous steps, we havePr µ( λ) -µ(λ * ) > δ ≤ 2 exp      - δ -σ √ d[B(τ ) -A(τ, δ)] 2 36σ 2      , provided t ≥ σ √ d[B(τ ) -A(τ, δ)]. Now for any s ≥ 0 and t ≥ 2e s 2 mη 2 , it holdsA(τ, s) ≥ (σ/σ) 1 -τ 2 s =: A(τ )s.In particular, ift ≥ 2e s 2 mη 2 + σ √ d[B(τ ) -A(τ )s] =: C, we have Pr µ( λ) -µ(λ * ) > δ ≤ 4 exp      - δ -σ √ d[B(τ ) -A(τ )s] 2 36σ 2     .Integrating the probability givesE[µ( λ) -µ(λ * )] = ∞ 0 Pr µ( λ) -µ(λ * ) > δ dδ = C 0 Pr µ( λ) -µ(λ * ) > δ dδ + ∞ C Pr µ( λ) -µ(λ * ) > δ dδ ≤ C + ∞ C exp      - δ -σ √ d[B(τ ) -A(τ )s] 2 36σ 2      dδ ≤ C + √ 36σ = 2e s 2 mη 2 + σ √ d[B(τ ) -A(τ )s] + 6σ.The bound can be optimized with respect to s, but the solution involves the Lambert W -function, which has no analytical expression. Instead choose s for simplicity ass = log σ 2mη 2 + .which givesE[µ( λ) -µ(λ * )] ≤ σ √ d 8 + B(τ ) -A(τ ) log σ 2mη 2 .Lemma D.1. Suppose that the J elements in Λ are drawn independently from a continuous density p with c := min ∥λ∥≤1 p(λ) > 0. Then with probability at least 1 -δ,η ≲ log(1/δ)/J 1/d, and with probability 1,η ≲ log(J)/J 1/d, for all J sufficiently large.Proof. We want to bound the probability that there is a λ such that |B(λ, η) ∩ Λ| = 0. In what follows λ is silently understood to have norm bounded by 1. Let λ 1 , . . . , λ N the centers of η/2-balls covering {∥λ∥ ≤ 1}, for which we may assume N ≤ (6/η) d . For λ k the closest center to λ, it holds∥λ ′ -λ∥ ≤ ∥λ ′ -λ k ∥ + ∥ λ k -λ∥ ≤ ∥λ ′ -λ k ∥ + η/2, so ∥λ ′ -λ k ∥ ≤ η/2 implies ∥λ ′ -λ∥ ≤ η. We thus have Pr(∃λ : |B(λ, η) ∩ Λ| = 0) = Pr inf λ J i=1 1{∥λ i -λ∥ ≤ η} ≤ 0 ≤ Pr min 1≤k≤N J i=1 1{∥λ i -λ k ∥ ≤ η/2} ≤ 0 . Further Pr min 1≤k≤N J i=1 1{∥λ i -λ k ∥ ≤ η/2} ≤ 0 = Pr max 1≤k≤N J i=1 -1{∥λ i -λ k ∥ ≤ η/2} ≥ 0 ≤ Pr max 1≤k≤N J i=1 E 1{∥λ i -λ k ∥ ≤ η/2} -1{∥λ i -λ k ∥ ≤ η/2} ≥ J inf λ E [1{∥λ i -λ∥ ≤ η/2}] .It holdsE [1{∥λ i -λ∥ ≤ η/2}] = Pr (∥λ i -λ∥ ≤ η/2) = ∥λ ′ -λ∥≤η/2 p(λ ′ )dλ ′ ≥ c vol(B(0, η/2)) = cv d (η/2) d ,where v d = vol(B(0, 1)). Now the union bound and Hoeffding's inequality givePr min 1≤k≤N J i=1 1{∥λ i -λ k ∥ ≤ η/2} ≤ 0 ≤ N exp - Jc 2 v 2 d (η/2) 2d 2 ≤ (6/η) d exp - Jc 2 v 2 d (η/2) 2d 2 . Choosing η = 2 2 log(3 d √ Jcv d /δ)/ √ Jcv d 1/d gives Pr(∃λ : |B(λ, η) ∩ Λ| = 0) ≤ δ/ 2 log(3 d √ Jcv d ),which is bounded by δ when√ J ≥ e 1/2 /3 d cv d . Further, setting η = 2( 6 log(J)/ √ Jcv d ) 1/d gives Pr min 1≤k≤N J i=1 1{∥λ i -λ k ∥ ≤ η/2} ≤ 0 ≲ J -5/2 , so that ∞ J=1 Pr min 1≤j≤J min 1≤k≤N j i=1 1{∥λ i -λ k ∥ ≤ η/2} ≤ 0 ≤ ∞ J=1 J Pr min 1≤k≤N J i=1 1{∥λ i -λ k ∥ ≤ η/2} ≤ 0 ≲ ∞ J=1 1 J 3/2 < ∞.Now the Borel-Cantelli lemma (e.g., Kallenberg, 1997, Theorem 4.18 ) implies that, with probability 1, |B(λ, η) ∩ Λ| ≥ 1, for all J sufficiently large.Recall:(i) (holdout) Let M = 1 and I 1,j = I 1 for all j = 1, . . . , J, and some size-⌈αn⌉ index set I 1 . (ii) (reshuffled holdout) Let M = 1 and I 1,1 , . . . , I 1,J be independently drawn from the uniform distribution over all size-⌈αn⌉ subsets from {1, . . . , n}. (iii) (M -fold CV) Let α = 1/M and I 1 , . . . , I M be a disjoint partition of {1, . . . , n}, and I m,j = I m for all j = 1, . . . , J. (iv) (reshuffled M -fold CV) Let α = 1/M and (I 1,j , . . . , I M,j ), j = 1, . . . , J, be independently drawn from the uniform distribution over disjoint partitions of {1, . . . , n}. (v) (M -fold holdout) Let I m , m = 1, . . . , M , be independently drawn from the uniform distribution over size-⌈αn⌉ subsets of {1, . . . , n} and set I m,j = I m for all m = 1, . . . , M, j = 1, . . . , J. (vi) (reshuffled M -fold holdout) Let I m,j , m = 1, . . . , M, j = 1, . . . , J, be independently drawn from the uniform distribution over size-⌈αn⌉ subsets of {1, . . . , n}.Recallτ i,j,M = 1 nM 2 α 2 n s=1 M m=1 M m ′ =1 Pr(s ∈ I m,i ∩ I m ′ ,j ).For all schemes in the proposition, the probabilities are independent of the index s, so the average over s = 1, . . . , n can be omitted. We now verify the constants σ, τ from Table 1 .(i) It holds Pr(s ∈ I 1,i ∩ I 1,j ) = Pr(s ∈ I 1 ) = α. Hence, τ i,j,1 = 1/α = 1/α × 1 = σ 2 × τ 2 .(ii) (reshuffled holdout) This is a special case of part (vi) with M = 1.(iii) (M -fold CV) It holdsPr(s ∈ I m,i ∩ I m ′ ,j ) = Pr(s ∈ I m ∩ I m ′ ) = 1/M, m = m ′ , 0, m ̸ = m ′ .Only M probabilities in the double sum are non-zero, whenceτ i,j,M = 1 M 2 α 2 × M/M = 1/α 2 M 2 = 1 × 1 = σ 2 × τ 2 , where we used α = 1/M . (iv) (reshuffled M -fold CV) It holds Pr(s ∈ I m,i ∩ I m ′ ,j ) =        1/M, m = m ′ , i = j 0, m ̸ = m ′ , i = j 1/M 2 , m = m ′ , i ̸ = j 1/M 2 , m ̸ = m ′ , i ̸ = j.For i = j, only M probabilities in the double sum are non-zero. Also using α = 1/M , we getτ i,j,M = 1 M 2 α 2 × M × 1/M = 1 = σ 2 . For i ̸ = j, τ i,j,M = 1 M 2 α 2 × M 2 × 1/M 2 = 1 × 1 = σ 2 × τ 2 . (v) (M -fold holdout) It holds Pr(s ∈ I m,i ∩ I m ′ ,j ) = Pr(s ∈ I m ∩ I m ′ ) = α, m = m ′ , α 2 , else.This givesτ i,j,M = 1 M 2 α 2 × [M × α + (M -1)M × α 2 ] = [1/αM + (M -1)/M ] × 1 = σ 2 × τ 2 . for all i, j. (vi) (reshuffled M -fold holdout) It holds Pr(s ∈ I m,i ∩ I m ′ ,j ) = α, m = m ′ , i = j α 2 , else.For i = j, this givesτ i,j,M = 1 M 2 α 2 × [M × α + (M -1)M × α 2 ] = 1/αM + (M -1)/M. For i ̸ = j, τ i,j,M = 1 M 2 α 2 × (M 2 × α 2 ) = 1. This implies that (1) holds with σ 2 = 1/M α + (M -1)/M , τ 2 = 1/(1/M α + (M -1)/M ). Remark E.1.Although not technically covered by Theorem 2.1, performing independent bootstraps for each λ j correspond to reshuffled n-fold holdout with α = 1/n. Accordingly, σ ≈ √ 2 and τ ≈ 1/2.We list all datasets used in the benchmark experiments in Table 4 .Table 4 : List of datasets used in benchmark experiments. All information can be found on OpenML (Vanschoren et al., 2014) Note that datasets serve as data generating processes (DGPs; Hothorn et al., 2005) . As we are mostly concerned with the actual generalization performance of the final best HPC found during HPO based on validation performance we rely on a comparably large held out test set that is not used during HPO. We therefore use 5000 data points sampled from a DGP as an outer test set. To further be able to measure the generalization performance robustly for varying data sizes available during HPO, we construct concrete tasks based on the DGPs by sampling subsets of (train_valid; n) size 500, 1000 and 5000 from the DGPs. This results in 30 tasks in total (10 DGPS × 3 train_valid sizes). For more details and the concrete implementation of this procedure, see Appendix F.3. We also collected another 5000 data points as an external validation set, but did not use it. Therefore, we had to tighten the restriction to 10000 data points mentioned in the main paper to 15000 data points as the lower bound on data points. To allow for stronger variation over different replications, we decided to use 20000 as the final lower bound.Here we briefly present training pipeline details and search spaces of the learning algorithms used in our benchmark experiments.The funnel-shaped MLP is based on sklearn's MLP Classifier and is constructed in the following way: The hidden layer size for each layer is determined by num_layers and max_units. We start with max_units and half the number of units for every subsequent layer to create a funnel. max_batch_size is the largest power of 2 that is smaller than the number of training samples available. We use ReLU as activation function and train the network optimizing logloss as a loss function via SGD using a constant learning rate and Nesterov momentum for 100 epochs. Table 5 lists the search space (inspired from Zimmer et al. (2021) ) used during HPO.The Elastic Net is based on sklearn's Logistic Regression Classifier. We train it for a maximum of 1000 iterations using the "saga" solver. Table 6 lists the search space used during HPO.The XGBoost and CatBoost search spaces are listed in Table 7 and Table 8 , both inspired from their search spaces used in McElfresh et al. (2023) .For both the Elastic Net and Funnel MLP, missing values are imputed in the preprocessing pipeline (mean imputation for numerical features and adding a new level for categorical features). Categorical features are target encoded in a cross-validated manner using a 5-fold CV. Features are then scaled to zero mean and unit variance via a standard scaler. For XGBoost, we impute missing values for categorical features (adding a new level) and target encode them in a cross-validated manner using a 5-fold CV. For CatBoost, no preprocessing is performed.XGBoost and CatBoost models are trained for 2000 iterations and stop early if the validation loss (using the default internal loss function used during training, i.e., logloss) does not improve over a horizon of 20 iterations. For retraining the best configuration on the whole train and validation data, the number of boosting iterations is set to the number of iterations used to find the best validation performance prior to the stopping mechanism taking action.7 In the following, we outline the exact implementation of performing one HPO run for a given learning algorithm on a concrete task (dataset × train_valid size) and a given resampling. We release all code to replicate benchmark results and reproduce our analyses via https://github.com/slds-l mu/paper_2024_reshuffling. For a given replication (in total 10):1. We sample (without replacement) train_valid size (500, 1000 or 5000 points) and test size (always 5000) points from the DGP (i.e. a concrete dataset in Table 4 ). These are shared for every learning algorithm (i.e. all learning algorithms are evaluated on the same data).2. A given HPC is evaluated in the following way:• The resampling operates on the train validation8 set of size train_valid.• The learning algorithm is configured by the HPC.• The learning algorithm is trained on training splits and evaluated on validation splits according to the resampling strategy. In case reshuffling is turned on, the training and validation splits are recreated for every HPO. We compute the Accuracy, ROC AUC and logloss when using a random search and compute ROC AUC when using HEBO or SMAC3 and average performance over all folds for resamplings involving multiple folds. • For each HPC we then always re-train the model on all train_valid data being available and evaluate the model on the held-out test set to compute an outer estimate of generalization performance for each HPC (regardless of whether it is the incumbent for a given iteration or not).on the results obtained from the 5x 5-fold CV (by only considering the first repeat or the first fold for each of the five repeats).9 For running HEBO or SMAC3, each resampling (standard and reshuffled for holdout, 5-fold holdout, 5-fold CV, 5x 5-fold CV) has to be actually run due to the adaptive nature of BO.For the random search experiments, this results in 10 (DGPs) × 3 (train_valid sizes) × 4 (learning algorithms) × 2 (holdout or 5x 5-fold CV) × 2 (standard or reshuffled) × 10 (replications) = 4800 HPO runs,10 each involving the evaluation of 500 HPCs and each evaluation of an HPC involving either 2 (for holdout; due to retraining on train validation data) or 26 (for 5x 5-fold CV; due to retraining on train validation data) model fits. In summary, the random search experiments involve the evaluation of 2.4 Million HPCs with in total 33.6 Million model fits.Similarly, for the HEBO and SMAC3 experiments, this each results in 10 (DGPs) × 3 (train_valid sizes) × 4 (learning algorithms) × 4 (holdout, 5-fold CV, 5x 5-fold CV or 5-fold holdout) × 2 (standard or reshuffled) × 10 (replications) = 9600 HPO runs11 , each involving the evaluation of 250 HPCs and each evaluation of an HPC involving either 2 (for holdout; due to retraining on train validation data), 6 (for 5-fold CV or 5-fold holdout; due to retraining on train validation data) or 26 (for 5x 5-fold CV; due to retraining on train validation data) model fits. In summary, the HEBO and SMAC3 experiments each involve the evaluation of 2.4 Million HPCs with in total 24 Million model fits.We estimate our total compute time for the random search, HEBO and SMAC3 experiments to be roughly 11.86 CPU years. Benchmark experiments were run on an internal HPC cluster equipped with a mix of Intel Xeon E5-2670, Intel Xeon E5-2683 and Intel Xeon Gold 6330 instances. Jobs were scheduled to use a single CPU core and were allowed to use up to 16GB RAM. Total emissions are estimated to be an equivalent of roughly 6508.67 kg CO2.In this section, we provide additional visualizations of the results of our benchmark experiments.Figure 6 illustrates the trade-off between the final number of model fits required by different resamplings and the final average normalized test performance (AUC ROC) after running random search for a budget of 500 hyperparameter configurations. We can see that the reshuffled holdout on average comes close to the final test performance of the overall more expensive 5-fold CV.Below, we give an overview of the different types of additional analyses and visualizations we provide. Normalized metrics, i.e., normalized validation or test performance refer to the measure being scaled to [0, 1] based on the empirical observed minimum and maximum values obtained on the raw results level (ADTM; see Wistuba et al., 2018) . More concretely, for each scenario consisting of a learning algorithm that is run on a given task (dataset × train_valid size) given a certain performance metric, the performance values (validation or test) for all resamplings and optimizers are normalized on the replication level to [0, 1] by subtracting the empirical best value and dividing by the range of performance values. Therefore a normalized performance value of 0 is best and 1 is worst. Note that we additionally provide further aggregated results on the learning algorithm level and raw results of validation and test performance via https://github.com/slds-lmu/paper_2024_reshuffl ing.• Random search -Normalized validation performance in Figure 7 . -Normalized test performance in Figure 8 .-Improvement in test performance over 5-fold CV in Figure 9 .-Rank w.r.t. test performance in Figure 10 .• HEBO and SMAC3 vs. random search holdout -Normalized validation performance in Figure 11 .-Normalized test performance in Figure 12 .-Improvement in test performance over standard holdout in Figure 13 .-Rank w.r.t. test performance in Figure 14 .• HEBO and SMAC3 vs. random search 5-fold holdout -Normalized validation performance in Figure 15 .-Normalized test performance in Figure 16 .-Improvement in test performance over standard 5-fold holdout in Figure 17 .-Rank w.r.t. test performance in Figure 18 .• HEBO and SMAC3 vs. random search 5-fold CV -Normalized validation performance in Figure 19 .-Normalized test performance in Figure 20 .-Improvement in test performance over 5-fold CV in Figure 21 .-Rank w.r.t. test performance in Figure 22 .• HEBO and SMAC3 vs. random search 5x 5-fold CV -Normalized validation performance in Figure 23 .-Normalized test performance in Figure 24 .-Improvement in test performance over 5x 5-fold CV in Figure 25 .-Rank w.r.t. test performance in Figure 26 . Based on the 5x 5-fold CV results we further simulated different M -fold holdout resamplings (standard and reshuffled) by taking M repeats from the first fold of the 5x 5-fold CV. This allows us to get an understanding of the effect more folds have on M -fold holdout, especially in the context of reshuffling.Regarding normalized validation performance we observe that more folds generally result in a less optimistically biased validation performance (see Figure 27 ). Looking at normalized test performance (Figure 28 ) we observe the general trend that more folds result in better test performance -which is expected. Reshuffling generally results in better test performance compared to the standard resampling (with the exception of logloss where especially in the case of a single holdout, reshuffling can hurt generalization performance). This effect is smaller, the more folds are used, which is in line with our theoretical results presented in Table 1 . Looking at improvement compared to standard 5-fold holdout with respect to test performance and ranks with respect to test performance, we observe that often reshuffled 2-fold holdout results that are highly competitive with standard 3, 4 or 5-fold holdout. Justification: We outline our three main contributions in the introduction (Section 1). We do not discuss generalization in the introduction, but rather in the discussion in Section 5.Guidelines:• The answer NA means that the abstract and introduction do not include the claims made in the paper. • The abstract and/or introduction should clearly state the claims made, including the contributions made in the paper and important assumptions and limitations. A No or NA answer to this question will not be perceived well by the reviewers. • The claims made should match theoretical and experimental results, and reflect how much the results can be expected to generalize to other settings. • It is fine to include aspirational goals as motivation as long as it is clear that these goals are not attained by the paper. 
experiments compute resources: 
 Question: For each experiment, does the paper provide sufficient information on the computer resources (type of compute workers, memory, time of execution) needed to reproduce the experiments?Answer: [Yes] Justification: We provide details in Appendix F.4.Guidelines:• The answer NA means that the paper does not include experiments.• The paper should indicate the type of compute workers CPU or GPU, internal cluster, or cloud provider, including relevant memory and storage. • The paper should provide the amount of compute required for each of the individual experimental runs as well as estimate the total compute. • The paper should disclose whether the full research project required more compute than the experiments reported in the paper (e.g., preliminary or failed experiments that didn't make it into the paper). 
code of ethics: 
 Question: Does the research conducted in the paper conform, in every respect, with the NeurIPS Code of Ethics https://neurips.cc/public/EthicsGuidelines?Answer: [Yes] Justification: Our work provides a study on reshuffling data when estimating the generalization error in hyperparameter tuning. Therefore, our work is applicable wherever standard machine learning is applicable, and we do not see any ethical concerns in our method.Guidelines:• The answer NA means that the authors have not reviewed the NeurIPS Code of Ethics.• If the authors answer No, they should explain the special circumstances that require a deviation from the Code of Ethics. • The authors should make sure to preserve anonymity (e.g., if there is a special consideration due to laws or regulations in their jurisdiction). 
broader impacts: 
 Question: Does the paper discuss both potential positive societal impacts and negative societal impacts of the work performed?Answer: [NA] Justification: The paper conducts fundamental research that is not tied to particular applications, let alone deployment.Guidelines:• The answer NA means that there is no societal impact of the work performed.• If the authors answer NA or No, they should explain why their work has no societal impact or why the paper does not address societal impact. • Examples of negative societal impacts include potential malicious or unintended uses (e.g., disinformation, generating fake profiles, surveillance), fairness considerations (e.g., deployment of technologies that could make decisions that unfairly impact specific groups), privacy considerations, and security considerations. • The conference expects that many papers will be foundational research and not tied to particular applications, let alone deployments. However, if there is a direct path to any negative applications, the authors should point it out. For example, it is legitimate to point out that an improvement in the quality of generative models could be used to generate deepfakes for disinformation. On the other hand, it is not needed to point out that a generic algorithm for optimizing neural networks could enable people to train models that generate Deepfakes faster. • The authors should consider possible harms that could arise when the technology is being used as intended and functioning correctly, harms that could arise when the technology is being used as intended but gives incorrect results, and harms following from (intentional or unintentional) misuse of the technology. • If there are negative societal impacts, the authors could also discuss possible mitigation strategies (e.g., gated release of models, providing defenses in addition to attacks, mechanisms for monitoring misuse, mechanisms to monitor how a system learns from feedback over time, improving the efficiency and accessibility of ML). 
safeguards: 
 Question: Does the paper describe safeguards that have been put in place for responsible release of data or models that have a high risk for misuse (e.g., pretrained language models, image generators, or scraped datasets)?Answer: [NA] Justification: The paper conducts fundamental research that is not tied to particular applications, let alone deployment. The paper does not develop models that have a high risk for misuse.Guidelines:• The answer NA means that the paper poses no such risks.• Released models that have a high risk for misuse or dual-use should be released with necessary safeguards to allow for controlled use of the model, for example by requiring that users adhere to usage guidelines or restrictions to access the model or implementing safety filters. • Datasets that have been scraped from the Internet could pose safety risks. The authors should describe how they avoided releasing unsafe images. • We recognize that providing effective safeguards is challenging, and many papers do not require this, but we encourage authors to take this into account and make a best faith effort.12. Licenses for existing assets Question: Are the creators or original owners of assets (e.g., code, data, models), used in the paper, properly credited and are the license and terms of use explicitly mentioned and properly respected?Answer: [Yes] Question: Does the paper describe potential risks incurred by study participants, whether such risks were disclosed to the subjects, and whether Institutional Review Board (IRB) approvals (or an equivalent approval/review based on the requirements of your country or institution) were obtained? Answer: [NA] Justification: The paper does neither involve crowdsourcing nor research with human subjects.Guidelines:• The answer NA means that the paper does not involve crowdsourcing nor research with human subjects. • Depending on the country in which research is conducted, IRB approval (or equivalent) may be required for any human subjects research. If you obtained IRB approval, you should clearly state this in the paper. • We recognize that the procedures for this may vary significantly between institutions and locations, and we expect authors to adhere to the NeurIPS Code of Ethics and the guidelines for their institution. • For initial submissions, do not include any information that would break anonymity (if applicable), such as the institution conducting the review.We admit that these benchmark libraries implement efficient benchmarking methods such as surrogate(Eggensperger et al., 2018;Pfisterer et al., 2022) or tabular benchmarks(Pineda Arango et al., 2021). It would be possible to adapt them to return the test performance, however, changes in the HPO evaluation protocol, such as the one we propose, would not be feasible.6 This summary is not exhaustive but reflects the general consensus observed in widely-used software.For CV and repeated holdout we take the average number of boosting iterations over the models trained on the different folds.With train validation we refer to all data being available during HPO which is then further split by a resampling into train and validation sets.We even could have simulated the vanilla holdout from the 5x 5-fold CV experiments by choosing an arbitrary fold and repeat but choose not to do so, to have some sanity checks regarding our implementation by being able to compare the "true" holdout with a the simulated holdout.Note that we do not have to take the 3 different metrics into account because random search allows us to simulate runs for different metric post hoc.Note that HEBO and SMAC3 were only run for ROC AUC as the performance metric. 
 
 Appendix:  


Decision: After the initial review, rebuttal, and discussion, the reviewers remain split on their decisions, but I am inclined to recommend accepting the submission.  Given its novel theoretical insights and thorough empirical analysis of a simple yet not well studied modification to ubiquitous hyperparameter optimization methodologies, the results in this work can provide value to both theoreticians and practitioners.

As reviewers pointed out (and authors acknowledged in the rebuttal) the clarity of presentation should be improved in several places.  I additionally suggest giving a few concrete examples of learning algorithms / model families that meet the regularity conditions required for your analysis. The additional empirical results using SMAC should also be included in the final version.

Finally, as mentioned in the thoughtfully written Limitations section, the theoretical analysis applies only to the setting in the limit of infinite data. Any insights on the possibility of (or obvious roadblocks) to a finite sample analysis would be a valuable addition and helpful for future extensions of this work.

Reviews: review: paper_summary: paper_summary: The paper suggests the idea that reshuffling the splits for every configuration during the hyperparameter optimization can improve the generalization property. The paper derives the theoretical analysis to shows how reshuffling affects the asymptotic behaviour of the validation loss surface, and the paper also provides a bound on the expected regret in the limiting regime. Finally, the paper also conducts some experiments to demonstrate the effectiveness of the proposed approach.
strength_weakness: strength_weakness: Firstly, I have various concerns with the theoretical analysis conducted in the paper, in particular, I think they’re not rigorous. I list in the below some of my concerns regarding the theoretical analysis.
+ In Theorem 2.1, the “regularity conditions” need to be explicitly mentioned in the theorem (cannot be put in the appendix) because the theorem itself needs to be self-contained in the main paper.
+ In Theorem 2.1, it’s unclear whether the covariance matrix \Sigma exist (because it’s a limitation of an expression and what if that expression goes to infinity?). Furthermore, even when it exists, how is it related to n? If it is larger than O(n) then the theorem doesn’t have any meaning because it doesn’t show the convergence of \hat{\mu}(\lambda_j)? 
+ In the discussion of Theorem 2.1, I don’t understand why we have Eq. (1). More explanations need to be provided.
+ In Theorem 2.2, why can we assume that \hat{\mu} follows a Gaussian process model? Is this assumption used in existing literature? And does it make sense in practice? Furthermore, what are the limits of the terms B(\tau) and A(\tau) in the RHS of the equation in Theorem 2.2? Without any quantification of these terms, we cannot conclude anything about how far \mu(\hat{\lambda}) from \mu(\lambda^*)

Secondly, for the experiments, my main concern is that the paper only evaluates the performance of the reshuffling approach using one state-of-the-art BO method (HEBO). I think it should be evaluated on at least 2 state-of-the-art BO methods to clearly demonstrate the effectiveness of the proposed approach.
questions: questions: Please see my questions in the Weakness section.
limitations: limitations: The paper describes the limitations of their method in Section 5.
paper_summary: paper_summary: In hyperparameter optimization (HPO), individuals often use the same resampling for different configurations to ensure fair comparison. However, this fixed split may introduce bias into the optimization process, particularly after numerous evaluations, as it tends to favor configurations that align well with that specific split. This study systematically explores the effects of reshuffling on HPO performance through theoretical analysis, controlled simulation studies, and real dataset experiments. The authors highlight that reshuffling resampling splits during HPO can help find configurations with superior overall generalization, particularly in scenarios where the loss surface is flat and estimates are noisy. Experimental findings indicate that when holdout reshuffling is employed, the ultimate generalization performance often rivals that of 5-fold cross-validation in a broad array of settings.
strength_weakness: strength_weakness: 1. The authors use a large number of symbols in the paper, adding a notation table may be considered to enhance readability.
2. The authors primarily investigate the impact of reshuffling in resampling and HPO but do not propose novel methods. The actual implementation is simple, with $n\in\{500,1000,5000\}$. The authors could consider making improvements to reshuffling itself based on the analysis of dataset noise and surface to determine reshuffling strategies.
3. The paper could consider conducting experiments on a wider range of models (e.g., SVM), datasets (e.g., mnist and cifar10), and HPO methods (e.g., successive halving) to demonstrate the effects of reshuffling comprehensively.
questions: questions: 1. In practical applications, reshuffling implies an increase in time consumption. How do the different methods in the experiments of this paper perform in terms of time consumption? When the total time is constant, does using reshuffling have advantages over using only resampling, or what advantages does it have?
2. In the experiments of this paper, how do the methods perform on each dataset? Does reshuffling exhibit different performances on different datasets?
3. Successive halving, as a method that uses different sampling ratios in the optimization process, how does reshuffling perform in it?
limitations: limitations: Already discussed.
paper_summary: paper_summary: This paper studies the effect of reshuffling the splits over which hyper-parameter optimiazation is performed. Specifically, the authors provide theoretical guarantees on the generalization performance achieved via reshuffling and empirically demonstrate its impact both via simulation and benchmark experiments. Overall, the results demonstrate that reshuffling improves HPO performance according to the theoretical analysis.
strength_weakness: strength_weakness: See above for weaknesses
questions: questions: **a)** 
How do you derive Equation (1)? Are the observations that follow based only off of theorem 2.1 and Equation (1)? Or based on other equations and theorems?

&NewLine;  
**Comments:**

You should repeat (on the figures) the meaning of 500, 1000, and 5000. It would make it much easier to read/interpret the results.

It seems that if you were to plot something like mean test improvement as a function of the cost  of each HPO approach, the benefits of shuffling would be more visible. From the current plots, it is not clear that the advantage of trying to improve the performance of holdout (especially when there are better approaches, as you show) is that holdout is cheaper than these other (better performing) approaches.

&NewLine;  
**[minor comment / observation]**

[line 26] You should explicitly introduce the CV acronym

[line 204] repeated 'sized'
limitations: limitations: The authors adequately discussed the limitations of the work.
paper_summary: paper_summary: The standard protocol evaluates various hyperparameter configurations using a resampling estimate of the generalization error to guide optimization and select a final hyperparameter configuration. The authors argue that reshuffling the splits for every configuration often improves the final model’s generalization performance on unseen data. They provide a theoretical analysis explaining how reshuffling affects the asymptotic behavior of the validation loss surface and provides a bound on the expected regret in the limiting regime.

The paper also presents a simulation study confirming the theoretical results and demonstrates the practical usefulness of reshuffling in a large-scale, realistic hyperparameter optimization experiment. The authors found that reshuffling leads to test performances that are competitive with using fixed splits, and it drastically improves results for a single train-validation holdout protocol.
strength_weakness: strength_weakness: The effectiveness of reshuffling depends on dataset characteristics, such as its size, noise level, and correlation structure, which limits the usefulness of reshuffling.
questions: questions: I am interested in seeing how reshuffling performs on more complex benchmarks and with more sophisticated models, such as training Resnet on CIFAR-10/100 or Imagenet. Experiments in such realistic settings could further strengthen the results.
limitations: limitations: The authors acknowledge that the benefits of reshuffling may vary based on noise correlation and loss surface curvature. I believe that the authors have conducted enough discussion regarding the limitations of the paper
paper_summary: paper_summary: The paper presents a compelling investigation into the effects of reshuffling resampling splits on the generalization performance of hyperparameter optimization (HPO) strategies. Through a mix of theoretical analysis and empirical studies, the authors argue that reshuffling can lead to statistically significant improvements in model performance, especially when the loss surface is flat and its estimate is noisy.
strength_weakness: strength_weakness: Generalizability of Results: The experiments are somewhat limited in scope, focusing on specific types of data sets and HPO strategies. It would be beneficial to see broader testing across more varied data types and with different models to fully understand the generalizability of the results.
questions: questions: There is little discussion on the computational costs associated with reshuffling, which could be significant, especially in large-scale applications. Understanding this trade-off is crucial for practical adoption.
limitations: limitations: As mentioned in the paper.

Comments: title: Author Rebuttal Availible
comment: I'm not pushing to have the pseudo-code in. But I liked your simplistic formulation of the problem. I think that simplified view is a nice add-on.  Especially before going into the theoretical demonstrations or throughout the text to break away from the mathematical equations and notation. Sentences that describe the tasks/problems in a simplified away provide good break points for readers to absorb/digest all the information they've read until that point.

I see what you mean for holdout. I still believe that if the HPO problem is not defined on binary classification, I might have to test and compare multiple approaches. I don't think this demerits your current work/contribution. But I believe this is something that can be improved/studied in the future.
Thank you for addressing my comments. I will keep my current score.
PseudoCode: We can surely add it, if you think it improves readability, no problem.

Practical consideration/usage: We disagree here, please reconsider this:
Especially for holdout, there is a clear on average advantage using reshuffling. This is clearly demonstrated by our experiments. Staying with the current "state" / "recommendation"  (no reshuffling) means you will perform worse, in many experiments. Just because we provide a deeper theoretical analysis, which shows in which situations this is most beneficial, and because we currently cannot exactly pinpoint them in a practical manner, shouldn't have us ignore this piece of knowledge now. We think your criticism would be merited if the situations where resampling / HPO are improved are somewhat "specific and rare", and then we would not help the reader to identify these situations. But as explained above (and the paper) this is not the case.
Thank you for the additional plots and for the clarifications.

**Pseudo-code:** I understand the method is quite simple, but the theoretical study in the paper is quite complex, making something simple seem rather (and perhaps unnecessarily) complex. This can arguably be seen as a disadvantage, as simplicity is typically something hard to attain. 

**Practical consideration/usage:** although I see advantages in using resampling, from a users' point of view, if I wanted to benefit from reshuffling I would have to try and compare different methods to evaluate, empirically, which one worked best for my use-case/dataset in practice. This seems rather burdensome and impractical.
Dear Reviewers,

Thank you for your reviews and your time.  The authors have provided a rebuttal, answering specific questions that were raised and have also provided additional empirical observations.

Please take a careful look and follow up with additional questions and/or update your review as necessary. At the minimum indicate you have read and understood the feedback.

Also, please feel free to start a private discussion in a separate thread.

Thank you,
Area Chair for Submission 1124