acceptodds
Under review as a conference paper at ICLR 2027

Detecting Harm Before Data Pooling

Abstract

Pooling another center's data can lower a model's accuracy on its own population when the added data carry a distribution shift. We turn will adding this source help? into a decision a center can make before any joint training and without exchanging raw data. The recipient either pools when the donor is expected to improve its deployment performance, declines when the donor is expected to hurt it, or abstains when the available evidence is insufficient to make either decision. To enable this three-way decision, we define the recipient-specific pooling effect as the change in the recipient's deployment performance that would result from adding the donor's data to its training set, and estimate it using a single aggregated gradient returned by the donor at the recipient's model. This allows the recipient to assess the prospective effect of pooling without accessing the donor's raw records or performing joint training. We provide guarantees for detecting harmful pooling and reducing decision costs under stated conditions. Across five datasets spanning synthetic, natural-image, and medical-imaging settings, our method more accurately identifies beneficial and harmful data additions than baseline approaches and yields reliable pool, decline, and abstain decisions across varying levels of distribution shift.

Primary area:
other topics in machine learning (i.e., none of the above)
Keywords:
data addition dilemma, data pooling, prospective assessment

Reviews

Among:
Shape:
1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_sZqTOpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper asks whether a recipient center N, before any joint training and without seeing raw data, can predict whether adding a donor center M's data will improve or degrade its model on its own population. The authors define the recipient-specific pooling effect Δ_true. They estimate it with a two-message protocol: N sends its fitted logistic model, and M returns its summed gradient g_M at that model. N then combines g_M with its own diagonal Fisher and a Fisher-normalized validation gradient. The result is a score with a first-order term and a nonnegative curvature term, obtained from a one-step influence displacement and a second-order expansion of recipient risk. A recipient-only bootstrap (donor message held fixed) gives a scale, and the rule pools, declines, or abstains according. Theoretical and experimental claims supports the overall narrative of the paper.

Critical strengths
  1. Correct target quantity. The paper isolates the right object: a signed, recipient-specific, counterfactual risk change rather than a distributional discrepancy. The argument for why discrepancy measures answer a different question is convincing and is borne out empirically. This is a genuine clarification relative to the Data Addition Dilemma line of work, which ranks sources by discrepancy.

  2. Compelling curvature result. The explanation (Prop. 1, App. A.13) is simple and correct. The ablations are convincing: the first-order term stays at 0.45–0.63 accuracy as n₁ grows on Toy and degrades to 0.458 on Toy-Op, while the full score reaches 0.94–1.0. This sharpens what Basu et al. (2020) and Koh et al. (2019) leave implicit: second-order group influence on parameters is not the same as second-order change in target risk.

  3. Lightweight, practical protocol. The protocol needs one O(d) message each way and O(d) scoring after an O(n₁d) Fisher diagonal. Because the full-Hessian variant is shown to add little, the diagonal approximation is empirically justified rather than merely asserted.

  4. Honest scoping of the theory. The assumption accounting (App. A.1, A.11), the explicit statement that A4 is assumed rather than proved, the admission that Thm. 1 certifies harm but never benefit, and the separation of the fixed-donor and local-shift bootstrap analyses are unusually careful. The privacy appendix is also careful about adjacency with no overclaims.

  5. Decision-theoretic evaluation. Danger versus over-caution errors, cost curves against trivial rules, and break-even abstention costs are more meaningful than AUROC alone for this application.

Critical weaknesses

1. Missing pooling baselines. Matching-based pooling (https://arxiv.org/pdf/2602.07154) admits donor data relative to a target centroid, at the domain level in its theory and at the sample level in its implementation, rather than discarding a donor entirely. The proposed rule is all-or-nothing: a ‘decline’ discards the entire donor even if most of it is compatible, which is wasteful when curation is expensive. A protocol-compatible variant seems feasible: the recipient sends a feature centroid along with θ_N, and the donor filters locally and returns the gradient over its retained subset, which is still two messages. How does the pooling effect of such filtered donors compare with the decline decisions?

2. The method can certify harm but not benefit, yet is framed as a pool/decline/abstain rule. The paper states this clearly in places: Thm. 1 recovers only positive signs, and Cor. 3(ii) shows pool is unreachable under the theoretical threshold. The population score is always ≥ 0, so negative scores arise only from the finite-sample first-order term, which the paper itself shows is weak. The benefit channel, term (B) in Lemma 10 (baseline excess risk ~d/n₁), is not represented in the score by any explicit variance-reduction term. The rule is therefore structurally biased toward declining, and the low danger rates are partly a consequence of this bias rather than evidence of discrimination. Two observations support this: κ ranges from 0.037 to 0.13 on Toy, so the score overestimates harm by roughly 8–25×, and DP noise inflates the score upward. The abstract and introduction should say plainly that the guarantees concern harm detection, and that "pool" decisions carry no guarantee in the fixed-donor regime.

3. Theory–experiment mismatch in the imaging settings. The guarantees assume unpenalized logistic fits with n₁ ≳ d (Lemma 1, Lemma 9). The imaging experiments use n₁ = 100 with frozen ResNet-50 embeddings, nominally d = 2048, so the unpenalized MLE generically does not exist. Appendix B.2 mentions "the same ridge term on its diagonal as ...," which suggests the deployed method is ridge-penalized, possibly after dimension reduction. Neither the ridge strength, its selection, nor any dimensionality reduction is reported in the main text. This matters in two ways: a) The theory does not cover the main experiments b) With a ridge term, the first-order optimality that makes the first-order term vanish at the baseline no longer holds in the same form. Please report d, the penalty, and its tuning, and state explicitly which results apply to the penalized estimator.

4. Abstention rates and break-even costs limit practical value. At k = 1, the rule abstains on 79–84% of trials on ISIC B, CheXpert, and Waterbirds, and the break-even abstention cost at r = 1 is 0.33–0.37. In the clinical scenario that motivates the paper, abstention means "collect more data" or "do the collaboration anyway." It is not obvious that abstaining in four of five cases is useful, especially when it must cost less than a third of a wrongly declined donor.

5. Evaluation labels and base rates. The help/hurt label is the sign of a loss difference on an evaluation fold of n_eval = 300 (150 for ISIC A). Many true effects are near zero, so the label is itself noisy. Base rates are highly skewed: 0.869 hurt on Toy, 0.802 on MNIST-Bar, 0.78 on ISIC A, 0.26 on Waterbirds. An effect-size-stratified analysis would clarify whether the method is detecting meaningful harm or mostly separating large-shift donors from clean ones. Examples include accuracy as a function of |Δ_true|, or AUROC excluding |Δ_true| below a tolerance.

6. The fixed pooling weight limits relevance. The decision is evaluated only at α = m/(n₁+m). In practice, and in the transfer-learning literature, one would reweight or shrink toward the recipient, under which "decline" is rarely optimal. The limitations section mentions this, but it weakens the practical motivation: a donor that harms at α = 0.8 may help substantially at α = 0.2.

Questions for authors

Please see "Critical Weaknesses" section of the review above. The paper is interesting and approaches the problem in a different way. I am keen to see the authors' response and am eager to revise my rating if the response addresses all my concerns.

Reviewer_Ch5EOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper wants to make a decision framework of whether including another source would help. The recipient of the data can pool if the data helps with the performance or decline if the data does not help. The paper call this framework to be recipient-specific pooling effect, which allows the recipient to assess the effect of the data before training. They tested it on the natural-image and medical image and find their method accurately identifies beneficial and harmful data.

Critical strengths
  1. The research topic itself (e.g., data valuation and selection) is meaningful.
  2. The uncertain category beyond harmful and helpful is interesting, although we are not sure how meaningful it is in practice.
Critical weaknesses
  1. The paper does not clearly differentiate their contribution from negative transfer, out-of-distribution data selection, continue learning and federated learning (as this paper mentions the centers). This problem formulation is not entirely new and previous studies have already investigated the data-source selection, harmful effects of additional data and selective collaboration among heterogeneous clients. I provide [1][2][3][4][5] for author to refer but broad transfer learning and continue learning should have already address this problem well in different perspectives. Leveraging the gradient to data selection is a well-known trick in this domain and this is the main concern of this paper. It does not provide comprehensive literature review as well as show these well known method.
  2. When the paper estimate the pooling effect, there is no good motivation of why the decomposition of first-order term and the curvature term make sense. I think GEM uses a more intuitive idea of leveraging gradient of a new task and gradients from earlier tasks to detect potentially harmful updates [5]. The paper does not show grounding before making the method and the theoretical analysis.
  3. The way of constructing labels by retraining the model with the new data and measure the difference in recipient loss on new held-out set is too experimental and lack practical consideration. The paper uses the small evaluation folds to make the cost low, but such way does not eliminate the sampling noise as well as cost of the algorithm. It would be nice if the author could consider using the full dataset (e.g., different full dataset in Xray domain or similar) to make sure their algorithm actually works.
  4. Similar for the experimental setting of logistic regression and linear probing, which is too experimental for the potential applicability in practice. It would be nice if the paper could consider focus their experimental setting with end-to-end neural network and even practical foundation model training that people use nowadays, where this problem formulation matters there.

[1] Data Valuation and Detections in Federated Learning [2] Game of Gradients: Mitigating Irrelevant Clients in Federated Learning [3] Data Valuation with Gradient Similarity [4] Detect, Decide, Unlearn: A Transfer-Aware Framework for Continual Learning [5] Gradient Episodic Memory for Continual Learning

Questions for authors
  1. Please provide a comprehensive literature review and position your work after the review. After this, is the paper still contributing to a novel part?
  2. What is the motivation for your method?
  3. What is the performance if the paper scales up the experiment?
  4. What is the performance if the paper scales up the model?
Reviewer_aiqBOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The authors tackle the problem of predicting whether adding another center's labeled data into joint training will improve the performance of the model on your own center. For logistic regression, they propose a which is a second-order approximation of the influence, computed from one gradient at the donor site and local data. The paper provides a theoretical characterization of this approach, followed by empirical evaluations on synthetic and real-world datasets.

Critical strengths
  • The paper tackles an important real-world problem, and proposes a theoretically justified approach.

  • The authors evaluate a wide range of baselines on a diverse set of imaging datasets.

Critical weaknesses
  1. The setup of the problem seems somewhat contrived, and the authors should further motivate it. Here, the donor is able to send the gradient vector (which doesn't have any privacy guarantees) to the recipient at a model of the recipient's choice, but not the full dataset right away (otherwise, the recipient can just try training with and without the new data). Why is this intermediate level of sharing the most practical? For example, since gradient are allowed to be shared, the two can also just learn a federated model, and compare against the one trained only on the target.

  2. All theoretical results are specific to unpenalized binary logistic regression, and the experiments are limited to linear probes on frozen encoders. The authors should assess whether the proposed method also works empirically for more complex and practical models like tree-based models and neural networks.

  3. The help-vs-hurt AUROC hides one aspect of the score, since AUROC is only a ranking metric. The authors should additionally report the decision accuracy for the signed scores after thresholding.

  4. There are some issues with the evaluation of the abstention component. Good abstention should defer when the true effect is small, and so the authors should compare the distribution of Δtrue\Delta_{true} on abstained versus committed decisions. Further, the authors should show the standard plot of error rate in committed trials versus k.

  5. The authors should add a clinical tabular dataset such as eICU to the empirical evaluations, since it is another common modality of data sharing, and has been studied in prior work such as Shen et al. (2024).

Questions for authors
  1. Please provide more details on the bootstrapping procedure to set the abstention threshold. Does each replicate involve the donor providing a new gradient at the new parameter value?

  2. The help-vs-hurt AUROC is not perfect even in the toy setting. Why do the authors think this is the case, and is it possible to attribute the different sources of error to the assumptions/approximations in the method?

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

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