IEL: Intra-Model Ensemble Learning For Single Sample Test-Time Adaptation

1. There is insufficient justification for minimizing the ensemble diversity. Personally, I believe that as diversity increases, performance can be improved in general including TTA since the information is also increases. For example, in [1] which is also referenced in this manuscript, it was shown that increasing diversity can lead to a lower loss. Additionally, the counterexample of ensemble of models with 100% performance (Lines 161–166) is unrealistic and therefore inappropriate for supporting the claim. If there is a large distribution shift and the source-trained models perform poorly on target dataset, reducing diversity may actually have an adverse effect. In conclusion, it remains unclear how reducing ensemble diversity benefits TTA.

2. Due to multiple assumptions, the scope of application of this research is limited. The authors assume there are multiple source-trained models (Lines 230–232), but it is questionable whether this assumption is easily met in practice. Furthermore, the assumption of stationary distribution shifts (Line 265-266) raises concerns about whether IEL would be effective in other TTA scenarios such as online imbalanced label distribution shifts or mixed distribution shifts [2].

3. The experiments conducted do not sufficiently demonstrate the effectiveness of IEL. For example, the authors should include 1) performance comparisons with various previous works on TTA, 2) ablation study on the number of ensemble models, and 3) comparisons of computational costs associated with using multiple models. As mentioned earlier, including experiments across diverse TTA scenarios would also provide a more comprehensive understanding of IEL’s effectiveness.

[1] A unified theory of diversity in ensemble learning [2] Towards stable test-time adaptation in dynamic wild world

Unfortunately, the submission has a number of weaknesses.

• incomplete method

The method works iteratively but the submission does not provide a termination condition. This is a not minor issue, as the manuscript makes it sound: without a termination condition, the method cannot be run in practice, and because no labeled data is available at test time, standard techniques, such as checking for a drop of validation accuracy, cannot be applied, either.

• lack of clarity in contribution and scientific comparison to prior work

The submission almost exclusively showcases the proposed method itself, but it does not put the method into context and competition with prior or alternative techniques. This leaves the novelty and relevance of the contribution unclear. Specifically, for a publication at a scientific venue, I expect that the novel aspect of the proposed method is clearly described, contrasting it to ideas and techniques that already existed in previous works. The manuscript does not do a good enough job doing so. As related work it concentrates almost exclusively on recent papers from the application domain of test-time adaptation with deep networks. However, ensemble methods have been studied extensively in machine learning, e.g. [Alaydin, "Introduction to Machine Learning", 2014; Chapter 17], and self-training methods for learning from unlabeled data also have a long history, going back at least to [Fralick, "Learning to Recognize Patterns without a Teacher", 1965], and having emerged many times afters, e.g. in the context of semi-supervised learning (e.g. Chapelle "Semi-Supervised Learning", 2006) and also test-time adaptation, e.g. [Royer et al, "Classifier adaptation at prediction time", 2015] . Even for adapting ensemble methods self-training was proposed before, e.g. [Ghosh et al, "Self Training with Ensemble of Teacher Models", 2021]. In light of extensive prior work, the manuscript should make clear what the technical novelty of the proposed method is.

• lack of baselines in experiments

The experiments evaluation presents results for the proposed method, but it does not contrast them against prior works. Consequently, the reader only learns that using proposed method often (but not always) works better than not doing test-time adaptation, but if the method is better than already existing methods for test-time-adaptation. It would also be important to see at least a comparison to obvious baselines, such simply self-training each network individually. For the specific choices made, e.g. using the majority vote prediction as target label but the softmax scores of the most confidence classifier, an ablation study would be needed if this is actually useful, or if maybe using hard labels or the ensemble average confidence would work equally well (or better).

• unsubstantiated claims

The manuscript contains factual claims, e.g. about design choices that are not self-evident but also not substantiated with evidence. Some of these appear misleading and/or are not credible, see "Questions". The counterexample on page 4 seems to be a misunderstanding of prior work. Claims in the literature are not that diversity is necessary for a good ensemble. Indeed, as the submission states, an ensemble consisting of many copies of a perfect classifier are still perfect. But rather, diversity of prediction mistakes between models in an ensemble can provably beneficial accuracy. Without any errors, that notion is not defined. But if mistakes do occur, the variance of predictions is decreased if errors are negative correlated (e.g. (17.5) in [Alpaydin, 2014]).

• shortcomings in the experimental protocol

Several aspects about the experimental evaluation are unclear or misleading (see questions below).

• The reported accuracy value in Tables 1-3 are "highest accuracy improvements" over all epochs. That means they are not unbiased estimates, but potentially overconfident.
• The description of ensemble elements is not clear from the text, it currently seems only provided in the Table headers.
• The specified regularization constant $\alpha=10e^{-11}$ (which should probably be $\alpha=10^{-11}$) is so small that no regularizing effect is mathematically possible even after hundreds of thousands of steps. I would expect $\alpha=0$ to work equally well.
• The exact variant of "ImageNet" dataset used is not clear. Best provide a source how the data was obtained and prepared.
• The results table lists differences in accuracy, but not absolute accuracy numbers, which would be useful to judge e.g. if the base classifiers are suitable for the task.
• It is not specified how the method's hyper-parameters were selected.
• Given the mixed positive and negative results, a test of significance should be performed if the reported results are not equally well explained by random chance (e.g. Wilcoxon signed rank).

Further comments:

• I found the analogies with human learning or research (for example the top of page 3) rather superficial, and I would recommend to remove those.
• The reference section should be corrected. Many papers are listed as arXiv or without publication venue, which actually have been published, e.g. [Arazo et al, IJCNN 2020], [Bucila etal, KDD 2006], ...

Summary

The presentation and investigation done in the paper is well below the bar for ICLR. There are no baselines, and the results are not well presented and contextualised. The introduction to the paper is lengthy, and should be made more crisp. The contribution statement is not accurate and needs to be adapted to what is actually shown in the paper. A lot of important controls and analysis experiments are missing to back up the claims. While I think that the general idea has potential, it needs a much better investigation to be considered for acceptance. A list of actionable points is given below.

For full transparency, while I would be happy to increase the score if my points are addressed, I doubt this is doable within the rebuttal period. Depending on the other reviews, I would already suggest that the authors consider a full revision of the paper and submission of their paper to the next conference. That being said, I think this could become a very nice paper if more work is spent on the experiments, and I would be happy to iterated with the authors during the discussion period.

Major

W1 There is a very lengthy introduction. The method section only starts on page 5. Before, a fair amount of related work is cited (great), but without considering any of that later as methods for comparisons.

W2 A naiive baseline is omitted: What happens if a state-of-the-art adaptation technique like EATA, or even older/simpler techniques like TENT are used, but adapting $n$ models in parallel, and then ensembling of the outputs?

W3 Section 3 needs a rewrite and improvements to clarity. For example, basic metrics like the cross-entropy loss are abbreviated with an extra symbol $\delta$, it would be better to clearly define the loss formulation used instead.

W4 The contributions reference “continual learning” (l. 130, l. 134), but there is no experiment backing this up. The reference should be removed.

W5 Claim 3 in the contributions (ll. 135-136) states that TTA requires a full batch. This is misleading or even wrong. There are certainly techniques that measure improvements when only a single sample is available (= model is adapted on that sample, and performance is measured) before the domain changes (e.g. Batch norm adaptation, or MEMO). However, in the setting considered here, model updates still accumulate on the same domain. In that setting, any TTA technique, like TENT, can be made suitable for the discussed setting by only updating every N steps (where N is the batch size), collecting the samples in the meantime.

W6 Claim 4 in the contributions is not at all corroborated by results in the paper and should be dropped.

W7 The paper needs to add recent methods to compare to. The current tables provide a lot of irrelevant details, and should be compressed. Instead of listing all different domains, it would be better to run a sufficient number of baseline models on the considered datasets to contrast the results. When doing so, it could be interesting to investigate whether the ensembling mechanism proposed is orthogonal to other adaptation methods: E.g., if we consider the EATA loss function for ensembling, does this improve over EATA?

W8 Analysis should be added: What happens if the number of models in the ensemble varies? How robust is this technique to common problem in cross-entropy based adaptation (model collapse) when training over long time intervals?

W9 In case the authors decide to keep the continual learning claim: How does the model perform in the continual adaptation settings used in CoTTA or EATA, and how does the model perform on long-term adaptation on CCC (Press et al., 2023)?

Minor

• Related work in l. 178: Batch norm adaptation (Schneider et al., 2020) re-estimates batch norm statistics, and this was shown to also work on single samples. Test time training (Sun et al., 2019) also considers single samples. TENT, in contrast, additionally performs entropy minimisation akin to the cross-entropy loss discussed in the study.
• Figure 1 misses a legend. The color code could be adapted, and e.g. corruptions of the same type could get the same color with different marker colours. That would make the plot more interpretable than the current 15 random colours.

• The proposed algorithm offers no substantial improvement over existing ensemble learning methods. It simply combines 1) selecting the most confident prediction and 2) cross-entropy minimization of ensemble models. Technical contributions to both ensemble learning and single-sample TTA remain limited.
• The paper lacks sufficient experimentation to demonstrate the proposed method’s effectiveness. It only compares results across different backbone architectures, without considering other baseline methods suitable for single-sample TTA, such as NOTE [1] and REALM [2]. Additionally, it does not explore alternative TTA settings, such as continual TTA, where incoming domains continuously change.
• The experiment section (Sec. 4) requires more careful writing and clarification. For instance, it should include a clear definition and detailed description of the tuning set samples, as well as more comprehensive experiments, including ablation studies, to examine the correlation between the number of ensemble models and TTA performance.
• In Section 4.1, the authors state that no catastrophic forgetting was observed on the ImageNet-C dataset. However, this is unlikely to be accurate since only 7,000 samples per corruption type from ImageNet-C were used for evaluation. More rigorous experiments and substantiated claims are needed.
• As noted in the limitations, the proposed method requires significant computational resources to utilize multiple pre-trained networks. However, the paper does not provide any empirical analysis or comparison of computational cost or adaptation latency.

[1] Gong et al., Note: Robust continual test-time adaptation against temporal correlation. NeurIPS'22.
[2] Seto et al., REALM: Robust Entropy Adaptive Loss Minimization for Improved Single-Sample Test-Time Adaptation. WACV'24.