acceptodds
Under review as a conference paper at ICLR 2027

Stable Accuracy, Unstable Allocations:Retraining Reproducibility in Selective Prediction

Abstract

Retraining a selective predictor can change which cases receive review even when accuracy changes little. We study the reproducibility of these review assignments under exact fixed-capacity top- selection, measuring allocation reproducibility (AR) by mean pairwise normalized review-set overlap. Across six visual settings with ten retrainings each, accuracy standard deviations are 0.11–0.50 percentage points, yet 37.6–50.1% of review slots are reassigned to different cases at a 10% budget. Civil Comments/DistilBERT shows lower turnover, at 11.3%. Changes affect persistent errors and also occur when predicted classes remain unchanged. We derive a sharp bound linking Spearman correlation to top- replacements, specialize an established subset-stability identity to connect set-level and individual disagreement, and characterize how realized score and cutoff changes constrain membership changes. Two-model probability averaging reduces median allocation turnover across all tested settings and budgets, but does not eliminate it. When review identity matters, accuracy and selective risk alone do not characterize the reproducibility of the resulting allocation.

Primary area:
other topics in machine learning (i.e., none of the above)
Keywords:
Selective prediction, Allocation reproducibility, Retraining instability, Top-\(k\) selection, Uncertainty estimation

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_9i5HOpenReview ↗
Rating
2
Confidence
2
Informativeness
1
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies whether retraining a selective predictor changes which of the samples are sent to review due to high uncertainty. The authors define allocation reproducibility (AR) as the overlap of top-k review sets and describe a sharp rank bound related to spearman correlation. They evaluate seven settings (six visual and one textual), each with ten retrainings. At a 10% budget, they find that roughly 38–50% of review slots turn over in the vision settings despite very low accuracy standard deviations, versus about 11% on Civil Comments. The turnover reaches persistent errors and cases whose predicted class never changes.

Critical strengths
  1. The problem is well-defined and the authors choose the right experimental protocol to test it. I don't necessarily agree with the choice of models and datasets (six visions against only a textual one), but the authors span their experiments through multiple seeds, which is appreciated. The authors also released code in their supplementary material.

  2. I commend the authors for the formal rigor and general clarity of the paper. From the introduction, the problem and problem setting are well presented.

Critical weaknesses

I list two critical issues that are core to my opinion. The first one is the applicability, or impact, of the study described in the paper. As per the author words, the field has long studied the effect on these classifiers with no interest in what samples exactly are sent for the review. However, the authors do not argue at all in the paper on why doing so is important. What has the field missed, so far? Why is studying the turnover of samples sent to review important? I fail to see the impact of this study, and its general framing in the literature, and thus the contribution appears to be marginal. Moreover, the paper does not present itself as a reusable benchmark, but more like an empirical study. This doubles down on the importance of making the reader understand what the impact will be.

My second concern is more technical. The authors use Corollary 1 as a "Spearman-certified overlap". To my understanding, this reverses Theorem 1, and says that given a strict-ranking Spearmak correlation ρ\rho, we can find an rmaxr_max max amount of review slots that have changed. The authors use the example of N=10,000 and k=1,000 with ρ=0.988\rho = 0.988 despite zero top-10% overlap. However, to my understanding, this example applies to the paper’s own results at 10% budget. The Spearman values in Table 1 are all below the threshold. So at the main budget, Corollary 1 guarantees no overlap at all in any setting, while the observed AR is 0.50–0.89. Since Corollary 1 is presented as a way to certify overlap, I would ask the authors to report what Corollary 1 actually guarantees on their data, next to the observed AR. If it is not guaranteeing anything, it should be reframed. In general, the paper spends a lot of space formalizing things, but it's not clear how many are actually needed.

Also, to compute the strict Spearman correlation between two runs, you need both rankings. If you have both rankings, can't you just count how many review slots match? What is the use of a bound?

Questions for authors

I refer the authors to the main two weaknesses that I raised.

1 comment
AuthorsOpenReview ↗

We clarify the practical significance of allocation reproducibility, report the empirical limitations of the Spearman bound, and distinguish its theoretical role from direct overlap measurement.

We thank the reviewer for recognizing the formal rigor and experimental protocol.

C1. Why does allocation reproducibility matter?

Aggregate performance does not reveal which cases receive limited review resources. Under fixed capacity, reviewing one case excludes another. Retraining can change these assignments even when accuracy and review capacity remain similar.

For example, after a content-moderation model is replaced, a persistently misclassified toxic comment may no longer receive human review despite similar aggregate accuracy. At the 10% budget, 37.6%–50.1% of review slots are reassigned across six visual settings. Among cases misclassified in at least eight of ten retrainings, 58.75%–83.97% change review status at least once. On Civil Comments, 27.26% of 2,487 persistently misclassified toxic comments change review status.

AR measures assignment consistency, while case-level analyses identify affected cases. We do not assume that every reassignment is harmful or that stability should always be maximized.

The released code provides a reusable evaluation protocol across models, uncertainty scores, and review budgets. We will clarify its practical motivation and scope.

C2. What does Corollary 1 actually guarantee?

The reviewer is correct that Corollary 1 provides no positive overlap guarantee for any of the 315 model pairs at the primary 10% budget.

Table 1 reports average-tie Spearman correlations, whereas the corollary requires strict rankings. We recomputed the bounds from the original predictions using deterministic tie-breaking across all 1,575 model-pair–budget comparisons. All 35 setting–budget AR estimates were reproduced, with no bound violations.

At the 10% budget:

SettingObserved ARMean lower boundPositive pairs
R18/C100.598100/45
R18/C1000.548600/45
R34/C100.584900/45
R34/C1000.499400/45
D121/C100.623800/45
R18/ImageNet-1000.545400/45
DBERT/Civil0.886800/45

The lower bounds are from Corollary 1; positive pairs have a strictly positive lower bound. A zero lower bound does not imply zero overlap; it means that Corollary 1 certifies no positive overlap for that comparison.

Across all budgets, 287/1,575 comparisons (18.22%) yield positive guarantees, exclusively at 20% and 30%. For Civil Comments, the mean lower bounds are 0.3399 and 0.5599, respectively, with 45/45 positive pairs at both budgets.

Mathematical sharpness does not imply empirical informativeness. We will report these results and present Corollary 1 as a worst-case bound, explicitly acknowledging its vacuity at the primary budget.

C3. Why use a bound when overlap can be computed directly?

Direct top-kk overlap is exact and preferable when both rankings are available. Corollary 1 offers no computational advantage.

Theorem 1 instead establishes what global ranking agreement alone guarantees about allocation. Its sharp construction shows that, with 10,000 cases and a 10% budget, Spearman correlation near 0.988 can coexist with completely disjoint selections. This explains why global ranking agreement cannot generally substitute for direct allocation evaluation.

Proposition 3 serves a different purpose: it localizes possible membership changes through realized score and cutoff movements. Its post-hoc bounds are nontrivial in 1,519/1,575 comparisons (96.44%), with mean clipped slack 0.0583.

We will distinguish these roles, report the empirical limitations of Corollary 1, and streamline the theoretical presentation.

Reviewer_nKk6OpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
1
Soundness
2
Read review
Paper summary

The paper presents an analysis of selective prediction stability: the authors show that when models are retrained, the set of instances that are rejected is unstable, despite overall accuracy varying less.

Critical strengths

The main strengths are:

  • the mathematical proofs seem correct, even though I might have missed something due to the very bad presentation of results/proofs
  • the experiments are quite extensive
Critical weaknesses

I have several concerns regarding this work.

  • Novelty. I am not really sure this work comes as novel, as the fact that the models are not stable when re-trained is quite well-established (see e.g., the predictive multiplicity phenomenon [1] ). Thus, I am not really surprised that the predicted probabilities can differ and, as a consequence, that the ML model does not provide a prediction for different instances once it is re-trained.

  • Significance. I do not understand in which practical case the model is not fixed at inference time, and thus, the allocation varies. Thus, from a practical perspective, I really do not see why one should be worried about the allocation identifiability gap. As far as I know, for standard selective predictors, one simply estimates a confidence threshold and abstains whenever confidence falls below that threshold [2]. Thus, at test time, the decision is always the same for a given input. Nevertheless, even assuming this is a concern, given that the model is different once retrained, I am not sure allocation stability is desirable, as each model should abstain in cases where it is less confident. Thus, it seems rather natural to me (and even desirable) that instances are not the same once the model is retrained (and confidence changes).

  • Presentation. The presentation is really not human-friendly. In my view, there are far too many acronyms, which make the reading very difficult. Second, some signs are not properly introduced (e.g., what is ρ\rho in Theorem 1? ). Then, the sections are not clearly separated, with some references to experimental settings across sections (e.g., line 156). Then, there is no intuition/description of the provided results (e.g., Proposition 1 and also Proposition 3 appear out of the blue). Generally speaking, the usage of paragraphs also makes the text quite painful to read. Finally, the presentation of results is just very difficult to follow.

Given the status of the paper, I am not able to support acceptance in the current status.

[1] - Watson-Daniels, J., Parkes, D. C., & Ustun, B. (2023, June). Predictive multiplicity in probabilistic classification. In Proceedings of the AAAI Conference on Artificial Intelligence (Vol. 37, No. 9, pp. 10306-10314).

[2] - Pugnana, A., Perini, L., Davis, J., & Ruggieri, S. (2024). Deep Neural Network Benchmarks for Selective Classification. J. Data-Centric Mach. Learn. Res., 1, 17-1.

Questions for authors

Please clarify my concerns. Especially, I think the paper would benefit from a careful re-writing from scratch (currently it is really difficult to follow). Moreover, I would like to understand better why the authors think allocation identifiability gap is a concern. Can the authors provide an example where this is actually concerning?

3 comments
AuthorsOpenReview ↗

We clarify the distinction between deterministic inference and retraining reproducibility, establish the practical significance and theoretical novelty of allocation-level analysis, and address presentation concerns.

We thank the reviewer for the feedback. All models in our study are fixed during inference. We compare review allocations across independently retrained models on the same cases. These are distinct settings: determinism within a model does not imply allocation reproducibility across models.

C1. Why does allocation reproducibility matter?

Consider 10,000 cases with capacity to review 1,000. Two deterministic models can achieve similar accuracy and select exactly 1,000 cases while assigning review to different cases.

Threshold-based selective classification [2] does not prevent this: retrained confidence functions may select different cases under fixed thresholds or matched coverage. Equal coverage does not imply equal allocation.

A concrete concern is the loss of review access for an unresolved error after model replacement. A toxic comment incorrectly classified as non-toxic may receive human review under the old model but remain unreviewed under its replacement. Similar aggregate accuracy does not reveal this change. In our Civil Comments experiment, at the 10% budget, 27.26% of 2,487 toxic comments misclassified in at least eight of ten retrainings change review status across runs. This is the practical concern behind the allocation identifiability gap: aggregate performance does not reveal which persistently misclassified cases retain access to review after model replacement.

C2. Distinction from predictive multiplicity.

Watson-Daniels et al. [1] study probabilistic prediction differences among near-optimal models. Our contribution quantifies exact fixed-capacity membership replacement under retraining.

Our sharp rank–allocation frontier establishes the minimum sum of squared rank displacements required for a given number of replacements. Its extremal construction shows that with 10,000 cases and a 10% budget, Spearman correlation near 0.988 can coexist with completely disjoint review sets. Probabilistic multiplicity alone does not establish this quantitative relationship.

Allocation turnover also differs from prediction churn. At the 10% budget, 1,156 of 8,903 R18/C10 cases whose predicted classes remain unchanged across all ten retrainings nevertheless change review status. Our pair-adaptive boundary certificate further localizes possible membership changes using observed score and cutoff movements. These quantitative allocation results are not established by [1].

C3. Potentially beneficial reassignments still warrant evaluation.

We agree that some reassignments may improve outcomes. Whether an allocation improves outcomes and whether it is reproducible are distinct evaluation questions.

At the 10% budget, the six visual settings exhibit 37.6%–50.1% review-slot turnover, despite accuracy standard deviations of only 0.11–0.50 percentage points. Among cases misclassified in at least eight of ten retrainings, 58.75%–83.97% change review status at least once.

AR measures assignment consistency; case-level analyses identify affected cases; accuracy and selective risk assess predictive utility. We report these together without equating turnover with harm or advocating stability regardless of predictive quality.

C4. Presentation.

We agree that the presentation can be clearer. We will reduce unnecessary acronyms and notation, define symbols—including Spearman's ρ\rho—before use, introduce Propositions 1 and 3 with intuition, and improve the organization of the experimental results.

We will also discuss Watson-Daniels et al. (2023) and Pugnana et al. (2024) in Related Work, clarifying how our fixed-capacity allocation analysis differs from predictive multiplicity and selective-classification benchmarking.

Could the authors please highlight the changes in the revised manuscript?

Thank you for the suggestion. We are preparing a version with the revisions highlighted and will upload it as soon as possible.

Reviewer_7ugMOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper presents a problem where multiple retraining results in similar accuracy but different sample-level allocation. The authors quantify the issue with Allocation Reproducibility under exact fixed-capacity top-k selection, derive a bound linking Spearman correlation to the replacement, and evaluate the bounds using certificates of membership changes.

Critical strengths
  • The problem is significant in extending the previous work on training variability to a selection/allocation level, bringing attention to sample membership that is often overlooked.
  • The theoretical formulation helps quantify how this issue presents in exact fixed-capacity top-k selection.
Critical weaknesses
  • The proposed algorithmic fixes like ensemble methods are not novel, and they do not fundamentally solve the issue from the theoretical point of view.
  • The experiments are limited in settings and are not clear about what demonstrates the validity or significance of the author contributions.
Questions for authors
  • What is the proposed solution for the introduced problem given the proposed quantification?
  • How would this work affect broader fields in ML?
1 comment
AuthorsOpenReview ↗

We clarify our theoretical and empirical contributions, distinguish them from standard mitigation methods, and discuss their broader relevance to fixed-budget selection in machine learning.

We thank the reviewer for the feedback.

C1. Novelty and scope of the mitigation method.

We agree that ensembling is not novel and provides no general guarantee of allocation stability. Two-model probability averaging is evaluated as a standard mitigation baseline, not an algorithmic contribution.

Our contribution characterizes allocation variability. We establish a sharp rank–allocation frontier and derive deterministic membership-stability certificates. We also specialize an established subset-stability identity to express allocation disagreement through case-level contributions. These results quantify what ranking agreement and score perturbations imply about allocation stability.

C2. What do the experiments establish?

Our evaluation covers seven model–dataset settings, 70 independent retrainings, and five review budgets, with an additional uncertainty-score robustness check.

The experiments establish three findings:

  • Magnitude and setting dependence. At the 10% budget, the six visual settings exhibit 37.6%–50.1% review-slot turnover despite closely matched accuracy, whereas Civil Comments has AR = 0.8868.
  • Case-level allocation changes. Review assignments change even among cases whose predicted classes remain unchanged and among cases misclassified in at least eight of ten retrainings.
  • Informativeness of the bounds. The pair-adaptive boundary bounds are nontrivial in 1,519/1,575 comparisons (96.44%), with mean clipped slack 0.0583 and no violations. By contrast, the Spearman-based bound provides no positive overlap guarantee at the primary 10% budget.

The 1,575 comparisons reuse the same 70 retrainings; they are not independent replicates.

C3. What solution follows from the quantification?

We provide a protocol for evaluating model replacements and stabilization methods at a fixed review budget. AR measures assignment consistency, case-level diagnostics identify which cases gain or lose review access, and the certificates characterize membership changes permitted by ranking or score information. These quantities complement accuracy and selective risk.

As a standard mitigation baseline, two-model probability averaging improves median AR in all 35 setting–budget combinations. It reduces turnover empirically but neither eliminates it nor provides a general stability guarantee.

C4. Implications for broader machine learning.

Batch active learning, data selection, and human-in-the-loop auditing also allocate limited resources using model scores. Retraining can change which samples receive labeling or review even when aggregate performance remains similar.

Our analysis applies to exact score-based fixed-capacity top-kk selection, regardless of model architecture or score source. It therefore provides tools for studying allocation reproducibility in these settings. Application-specific consequences and extensions beyond exact top-kk selection require further study.

We will clarify the role of the mitigation baseline and the purpose of each experiment.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

Related papers

Loading the map…

Discussion (0)

Sign in to comment.