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Under review as a conference paper at ICLR 2027

When Efficient Training Becomes Unfair: Auditing and Repairing Data Pruning

Abstract

Data pruning reduces training cost by removing examples a model appears to have learned, often with little change in average performance. However, average metrics can conceal substantial subgroup harm. First, we conduct a systematic demographic-fairness audit of data pruning across static and dynamic criteria and find that pruning can significantly degrade subgroup and worst-group performance even when removal is demographically uniform. This harm is not explained by preferential deletion of minority data; instead, pruning reduces overall training exposure, disproportionately affecting data-scarce groups. Motivated by this finding, we propose EquiPrune, a lightweight, modular wrapper that operates at the pruning decision stage to preserve sufficient training exposure. Across diverse datasets, architectures, and pruning strategies, EquiPrune restores baseline-level fairness in most affected settings while retaining substantial computational savings. These results suggest that efficient training should be evaluated on the fairness–efficiency frontier, not just accuracy–efficiency.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Data Pruning, Fairness, Training Efficiency, Efficient Deep Learning, Subgroup Robustness

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_o6aEOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

In this work, the authors illustrate that data pruning in an equitable fashion across represented subgroups can lead to unequal performance across subgroups with the final model. They motivate that this is an important phenomenon to address as conventional "average performance [metrics] alone [do] not reveal whether the resulting savings [from pruning] affect all demographic groups equally." After describing this problem and relevant notation, they show that it arises theoretically using "the standard power-law relation between data quantity and excess risk" and demonstrate that it holds empirically in most of the cases they evaluate in an audit (while attributing results in cases where it does not hold to large amounts of available data and relative dataset balance compared to the other cases). They additionally propose EquiPrune, a pruning method to address the shortcomings of demographics-blind pruning. Via ablation study of its three components, they find that the data retention floor component is most impactful in mitigating unequal performance while maintaining data efficiency (in addition to being demographic agnostic), but the other two components (which handle retention and rescaling of relevant subgroups) also help with this mitigation (though they are not demographic agnostic). They conclude by summarizing their work and its impact while acknowledging that improving the components that currently require demographic information is appropriate future work.

Critical strengths

This work tackles an important problem by proving that the problem exists theoretically and empirically, and they follow this analysis with an algorithm that takes major steps towards remedying the problem. Moreover, they perform ablation analysis of their proposed solution to study which parts of their approach are most impactful, and they additionally explore a setup with multiple protected attributes per example (not traditionally the norm in algorithmic fairness research). The experimental setup more generally is sensible and explores a Cartesian product of datasets, models, and optimization schemes.

Critical weaknesses

The primary drawback of this work is that its prose and organization were not always easy to understand. In particular, Figure 1, "the paper in one picture", is text-heavy and squeezed into the top corner of page 3 and only referenced on pages 4 and 5 despite serving as a visual summary of the work. Similarly, they describe the math behind their audit and proposed algorithm in Section 3 while they describe and analyze their experiments in Section 4. While this is not an incorrect approach, it was confusing to read about how "The audit yields a clear target: the pruner that saves the most also harms the most" and learn how EquiPrune works before seeing any of the results or supported/refuted hypotheses or predictions.

The authors also make use of several remark/point organization systems throughout their work (e.g., R1,R2 for research questions and Hsel,Hopt\mathrm{H_{sel},H_{opt}} for different hypotheses). Individually, these systems are helpful, but the authors use them simultaneously in a way that is sometimes confusing (e.g., in Section 4, "(D3) Exposure is equal...Hsel\mathrm{\mathbf{H}_{sel}} is accepted...In the worst regime, Black loses 5.07 AUC points against 3.29 for White, and across datasets the largest loss falls on a minority group (Figure 3, Appendix C.3), as prediction (P2) of Proposition 1 expects...The repair closes the loop: the demographics-blind floor alone, which bounds only how much is removed, passes R2 in five of nine regimes..."). Furthermore, it appears that this work would benefit from line breaks while introducing these systems and new ideas (e.g., the bolded "Fixed pre-registered decision rules." in Section 4 appears to be a paragraph header, but it itself is buried in the introductory paragraph of Section 4).

Lastly, it was clear to me that AI tooling was used to draft and organize this paper before I read the authors' statement asserting this. This in itself is not grounds for rejection, but one could also argue that sentences like "Data pruning is sold as a free lunch: the same accuracy for less data. We asked who pays for it.", headers like "Who is compromised, and what comes back", and other parts of the main body could have benefited from polishing and human review. This said, I found the abstract and Introduction strong and easy to read (to the extent that I am unsure whether AI assistance was used in drafting those sections). However, the portions with more obvious AI use, in conjunction with the organization issues mentioned above, are noticeable drawbacks of the work.

Questions for authors

I have the following questions for the authors beyond the points I mentioned above:

  • To your knowledge, do the distance metrics used as fairness metrics also run into statistical bias noted by Lum et al. (2022)?
  • How are (certain) hyperparameters for EquiPrune chosen?
    • For instance, why is ϕ\phi 0.15? (γ\gamma makes sense of 0.9 in the group-retention quota rule, but nothing is said about the absolute retention floor rule at least in the main body of the work)
    • I am aware of sensitivity analysis of these parameters, but it appears ϕ\phi was chosen a priori. How was this determination made? (More of a justification in the main body would also be welcome)
4 comments
AuthorsOpenReview ↗

Response to Reviewer o6aE (1/2)

We thank the reviewer for the positive assessment and for the detailed, actionable feedback on presentation. We answer the three weaknesses together, since they all concern how easy the paper is to read, and then the two questions.


W1–W3. Organization, overlapping labels, and wording that reads as AI-generated.

We agree with all three points, and we apologize for the wording. Phrases such as "Data pruning is sold as a free lunch… We asked who pays for it" and headers like "Who is compromised, and what comes back" were our attempt to make the trade-off concrete through analogy. We agree they came across as stylized rather than precise, and they did not suit a technical paper.

We went through the text. We replaced rhetorical phrasing with plain statements and made headers say what the paragraph contains, using the abstract and introduction, which the reviewer found clear, as the reference style. For example, the opening of the conclusion now reads "Data pruning is usually judged by how much data it saves at the same average accuracy. We studied how these savings affect demographic subgroups." The header "Who is compromised, and what comes back" is now "Per-group effects", the Figure 1 title "The paper in one picture" is now "Overview: the pruner, the audit, and the repair", and the guardrail summaries "Never train on almost nothing" and "Count what is left more heavily" now read "Keep a minimum amount of data" and "Up-weight the remaining data of under-retained groups". We also fixed several small inconsistencies and garbled sentences found during this pass.

Based on the complete discussion, we will address all the remaining points, and we will use the additional page to organize the paper better.

AuthorsOpenReview ↗

Response to Reviewer o6aE (2/2)

Q1. Do the distance-based fairness metrics suffer from the statistical bias noted by Lum et al. (2022)?

To the best of our knowledge, yes, in principle. ES-AUC, DPD, and DEOdds are spreads of noisy per-group estimates, so in finite samples they are biased toward larger disparity, most for small groups. Worst-group AUC is biased downward. Two features of our design limit the effect: every comparison is paired on the same test set and groups, and "Unknown" and very small groups are excluded from all gaps.

To check this directly, we estimated the bias of every run with a bootstrap (App. N). We resample the test patients with replacement 200 times and recompute the metric each time. The average difference between the resampled values and the original value estimates the bias, and subtracting it gives a bias-corrected value. All numbers below are in AUC points ×100.

  • What the bias is. The bias of ES-AUC is negative: −0.75 points on average for the unpruned baseline. In other words, finite-sample noise makes the measured ES-AUC about 0.75 points lower, i.e. the model looks slightly less fair, than it would with an unlimited test set. This is the effect Lum et al. describe.
  • Why it matters little for our conclusions. Our claims are about differences between a pruned model and the unpruned baseline on the same test set, not about absolute ES-AUC. The bias is about the same for both: −0.64 for B-PAS and −0.72 for EquiPrune, against −0.75 for the baseline (averages over all runs of each method). When we subtract the baseline from a pruned model, the two biases almost cancel; what remains is about 0.1 point, far smaller than the effects we report.
  • What happens after correction. We recomputed each difference from the bias-corrected values. For B-PAS on FairVLMed/R50+SGD (8 seeds), the change in ES-AUC relative to the baseline goes from −4.84 (uncorrected) to −4.88 (corrected), and the change in worst-group AUC from −5.60 to −6.60. Both are still clear losses, and the corrected losses are slightly larger. The same holds in the other regimes: no conclusion changes.

The uncorrected numbers in the paper therefore, if anything, slightly understate the harm. We report the corrected values in App. N.


Q2. How were EquiPrune's hyperparameters chosen; in particular, why φ = 0.15, and how was it chosen a priori?

  • How φ was fixed. The floor was introduced after a preliminary run on FairVLMed/R50+SGD, in which B-PAS reduced the active set to 1–4 of 54 batches for the last ~80 epochs. We then fixed φ = 0.15 (9 of 54 batches) before the nine-regime study and did not tune it per dataset or on test results. We have corrected Appendix B.4, which described all three values as chosen before any experiment.
  • What the floor is for. Our new analysis (App. O) shows that B-PAS's harm arises when it empties its active set and stops training at epoch ~108, while the learning rate is still at ~47% of its peak. The floor's main job is to keep enough batches for training to complete its schedule. Even a very small floor does this: φ = 0.05 (3 batches) already lands at −0.04 ES-AUC in the sensitivity sweep (App. K). The sweep is noisy at small floors (φ = 0.10 lands at −0.80), so φ = 0.15 adds a safety margin above that region while keeping ~56% savings.
  • The trade-off. Above that point, φ is a savings–safety dial. φ = 0.40 keeps more data at 43% savings, and φ = 0.15 keeps 56% (App. K). For practitioners, we suggest choosing φ so that the smallest protected group keeps a minimum number of samples per epoch, φ ≥ N_min / n_smallest-group.
  • γ = 0.9 and c = 5 are flat across their plausible ranges in the same sweep (γ ∈ [0.70, 0.95], c ∈ [2, 100]).

We will move this justification from the appendix into the main text, where EquiPrune is introduced; the supporting analysis is in App. O.

Reviewer_o6aEOpenReview ↗

Response to Author Rebuttals

I thank the authors for their engagement with my feedback and updates made to the draft in response to my comments. The reorganized paper is much clearer, and I appreciate the blue text highlighting crucial insertions. However, there are still a few paragraphs where additional line breaks could be helpful if allotted space allows for them (e.g., in the "Two hypotheses, and the instrumentation that separates them" paragraph to emphasize the hypotheses and the falsifiable predictions). As a more minor point, some of the blue text does not have adequate spacing before the normal text it follows (e.g., in the abstract, "modular wrapper that operates at the pruning decision stage to preserve sufficient training exposureand to let training complete its schedule"). Given that these lingering issues are minor, I will retain my overall positive score.

AuthorsOpenReview ↗

Follow-up Response to Reviewer o6aE

We thank the reviewer for the engagement, thoughtful review, and constructive discussion. The remaining suggestions and some other minor issues have already been addressed, and they are reflected in the updated manuscript. We expect the final version to be more organized and complete based on the overall discussion. We thank the reviewer again for helping us make the manuscript better.

Reviewer_srdcOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This paper investigates the impact of data pruning on model fairness and proposes EquiPrune, a lightweight wrapper intended to mitigate subgroup performance degradation while retaining computational savings.

Critical strengths
  1. The paper examines data pruning from a fairness perspective and argues that the observed harm does not arise from preferential removal of minority-group data. The problem is practically relevant.
  2. The authors present the experimental results clearly.
Critical weaknesses
  1. Insufficient statistical support for the audit conclusions. The authors conclude that data pruning harms fairness, but the audit results do not adequately support this conclusion. In several settings in Table 1, the standard deviations are comparable to or larger than the magnitudes of the mean changes, and the direction of change varies across settings. These results provide limited support for widespread and consistent fairness degradation.

  2. The effectiveness of EquiPrune and the value of its components remain unclear.

  • The repair reduces computational savings, yet there is no comparison against less aggressive pruning under the same computational budget.
  • The gains reported in Table 2 remain within the scale of the standard deviations, providing insufficient evidence of effectiveness.
  • None of the four variants, including the full EquiPrune method, meets the success criterion in more than five of the nine settings. Moreover, success is determined solely by whether the mean crosses a threshold of −0.5 points, a tolerance much smaller than the standard deviations in most settings. Adding Q and R to the basic F component sometimes further reduces performance. The consistent value of these additional components and the basis for selecting a variant in practice therefore remain unclear.
  1. The FairCLIP experiment provides limited evidence. The baseline AUC in Table 3 is only 53.91, close to random performance. Small fairness improvements over such a weak baseline are of limited significance.

  2. Limited task coverage. All experiments involve binary classification, with no evaluation on multiclass tasks. The broader applicability of the method remains insufficiently validated.

  3. Missing fairness baselines. The experiments compare fairness metrics only against other pruning methods, without comparisons to relevant fairness approaches such as fairness-aware data pruning (Zayed et al., 2023), FairBatch, and group DRO.

Questions for authors
  1. Under the same computational budget, does EquiPrune outperform simply reducing pruning aggressiveness? How can the gains from the repair mechanism be distinguished from those due to additional training?

  2. F alone often outperforms the full method. Under what conditions do Q and R help, and how should a variant be selected without relying on test results?

  3. Is the method effective on multiclass tasks, particularly when class imbalance and demographic-group imbalance coexist?

6 comments
AuthorsOpenReview ↗

Response to Reviewer srdc (1/3)

We thank the reviewer for the review. To address the statistical and methodological points, we ran several additional training runs, reported in four new appendix sections:

  • (App. M) compute-matched and less-aggressive pruning baselines;
  • (App. N) five additional seeds with 95% confidence intervals;
  • (App. O) an analysis of when the harm arises;
  • (App. P) a multiclass experiment.

We will use the additional page to reorganize the paper based on the discussion

Notation. Δ is the seed-paired change against the unpruned baseline, in AUC points ×100. A pair of numbers in square brackets after a value, e.g. −4.84 [−7.68, −2.00], is the 95% confidence interval of that value (a t-interval over seeds); an interval that lies entirely below (above) zero means the change is distinguishable from run-to-run noise. B-PAS threshold schedules are written differently, as "schedule [δ_start, δ_end]", e.g. [5e-6, 5e-5]; these brackets are threshold values, not confidence intervals.


W1. Insufficient statistical support: standard deviations comparable to the means; direction varies across settings.

Single cells with three seeds are noisy, and the paper says so (our t-tests are marked descriptive). The audit's conclusion rests on effects replicated across regimes, which we now quantify directly:

  • Pooled across regimes. A random-effects meta-analysis over all regimes gives a pooled B-PAS effect of −1.18 [−2.24, −0.12] ΔES-AUC (p = 0.029); all three pruners together give −0.28 [−0.51, −0.04] (p = 0.022).
  • More seeds where the effect is largest. On FairVLMed/R50+SGD with 8 seeds, B-PAS costs −4.84 [−7.68, −2.00] ES-AUC and −5.60 [−8.59, −2.62] worst-group AUC. Pooled over all 14 independent runs of this configuration, it costs −3.40 [−5.28, −1.52] (p < 0.01) (App. N).
  • Not a small-sample artifact. Re-scoring every run with a bootstrap bias correction for the fairness metrics leaves these effects unchanged or slightly larger (App. N).

The direction varying across settings is expected.

W2a / Q1. No comparison against less aggressive pruning under the same budget; how to separate the repair from additional training.

We added both comparisons (App. M) on FairVLMed/R50+SGD (5 seeds):

MethodSavingsΔAUCΔES-AUC
B-PAS, less aggressive [1e-5, 1e-4]~35%+0.03+0.51
Unpruned, schedule shortened to the same budget55%−0.17−0.15
EquiPrune-F55%−0.77+0.90
B-PAS, less aggressive [5e-5, 5e-4]~60%−1.96 (p<0.01)−0.63
B-PAS (default)~65%−4.76 (p<0.01)−5.29 [−10.44, −0.14]
  • Versus less aggressive pruning at matched savings, EquiPrune-F is better: +1.54 [+0.19, +2.88] ES-AUC against B-PAS tuned to ~60% savings, with less AUC loss.
  • Not additional training. At matched savings both methods use the same number of batch-epochs. What differs is when training ends. B-PAS empties its active set and stops at epoch ~108 with the learning rate still at ~47% of its peak. Across 91 B-PAS runs, the learning rate at the stopping point predicts the fairness loss (ρ = −0.32, p = 0.002) (App. O). EquiPrune's floor keeps a small set of batches until the schedule completes. The sensitivity sweep agrees: a floor of only 3 of 54 batches already lands at −0.04 ES-AUC (App. K).
  • Consistent with this, a compute-matched shortened schedule is also harmless and about as fair as EquiPrune (difference +1.06 [−1.60, +3.71]). We report it next to the pruning arms (App. M). EquiPrune's role is to make a dynamic pruner safe: it keeps the pruner's own signal and adaptive budget, and removes the failure mode that causes the harm.

W2b. Gains in Table 2 are within the standard deviations.

The right test pairs EquiPrune with the pruner it wraps, same seed and same signal, which removes baseline noise. With 8 seeds on FairVLMed/R50+SGD, EquiPrune minus B-PAS is +4.74 [+1.71, +7.78] (F+Q+R) and +5.49 [+2.08, +8.89] (floor only) (App. N). The independent generality study gives the same result: +3.96 ± 1.15, p = 0.027 (App. I). The benefit appears where the pruner causes harm and is near zero where it does not (App. I, "the benefit tracks the harm"), which is what a targeted repair should do.

AuthorsOpenReview ↗

Response to Reviewer srdc (2/3)

W2c / Q2. No variant passes more than 5/9; the −0.5 threshold is small; Q and R sometimes hurt; how to choose a variant without test results.

  • The threshold. The −0.5 tolerance was fixed before the experiments. App. K shows the repair verdict is unchanged when the tolerance is varied (0.25 / 0.5 / 1.0 points) together with the savings floor.
  • The variant. We agree that Q and R are not consistently helpful, and we take a clear position: the method is the floor F. It is demographics-free and passes the repair rule in five of nine regimes, more often than any other variant. Q and R are optional safeguards for the case where a pruner does select against a group, which our retention accounting tests for and did not find. This also matches Rolf et al. (ICML 2021). They find that group reweighting (importance weighting, group DRO) mainly compensates for a poorly allocated training set and helps less than having the data, and that importance weights become high-variance for very small groups. R is group importance weighting, with its weight clipped at c for that reason, so it is expected to add little once the floor keeps the data in training.
  • Choosing without test data. Retention accounting runs during training, so the choice needs no test results: enable Q/R only if a group's time-averaged retention falls behind the others. On the primary attribute this gap stays below 0.034 in every regime, so the rule selects F everywhere (App. O.1). Choosing per run by validation ES-AUC gives no consistent gain over always using F (App. O.1), which supports a fixed default.

W3. The FairCLIP baseline AUC (53.91) is close to random; small improvements over a weak baseline are of limited significance.

The FairCLIP experiment has a narrow purpose: to show that the pattern of harm and recovery also appears under a different objective (contrastive vision-language fine-tuning with a fairness regularizer), architecture and optimizer, with the pruning machinery and (φ, γ, c) unchanged. It is a within-setting, seed-paired comparison. All methods share the same port, data, prompts and evaluation, so the comparison is between pruning arms, not against the published FairCLIP numbers.

We acknowledge that our port's absolute AUC is below the published FairCLIP results. The gap is already present before any fine-tuning (zero-shot), so it lies in evaluation details common to all arms, upstream of any pruning decision. Within that fixed setting, the pattern matches the main study:

  • B-PAS lowers worst-group AUC on every attribute (race −1.17, gender −2.74, ethnicity −2.67, language −13.59).
  • EquiPrune improves on B-PAS for all four, at the same ~35% savings, and ends above the unpruned baseline for race (+0.87) and language (+1.33).

W4 / Q3. All experiments are binary classification; is the method effective on multiclass tasks, especially when class imbalance and group imbalance coexist?

Our question is about demographic fairness under data pruning, and the mechanism does not depend on the number of classes. Batch-level pruning removes random cross-sections of the data, which preserves class and group composition, and the guardrails act on group retention. To show this directly, (App. P) re-runs FairVision-AMD with its native four grades (normal / early / intermediate / late AMD) instead of the binary screening task, on the same images, seeds and fixed batches. This setting combines class imbalance (early and late AMD are rare) with race imbalance, as asked in Q3.

The results match the binary task. B-PAS changes ES-AUC by −0.90 [−4.42, +2.63] with four grades and by −1.01 [−3.16, +1.15] in the binary form, while costing 2.90 points of macro AUC and 4.04 points of balanced accuracy (both p < 0.01) at ~63% savings. EquiPrune recovers 1.58 AUC points over B-PAS [+0.99, +2.16]. The conclusions do not depend on the label space.


AuthorsOpenReview ↗

Response to Reviewer srdc (3/3)

W5. Missing fairness baselines (Zayed et al., 2023; FairBatch; group DRO).

These methods solve a different problem from ours, so they are not like-for-like baselines:

  • Group DRO and FairBatch improve fairness at full data cost, with 0% savings. EquiPrune addresses how to keep baseline fairness while pruning, and its reference point, the unpruned baseline, is in every table. The two are complementary: EquiPrune acts at the pruning decision and can wrap any training objective, including group DRO. Rolf et al. (ICML 2021) also find that such reweighting helps less than a better-allocated training set, which is what keeping the data in training (the floor) provides.
  • Zayed et al. (2023) prune counterfactually augmented text (gender-word swaps) to optimize parity metrics. Medical images have no counterfactual pairs, and App. G shows the parity metrics they optimize can improve while a pruned model degrades.

The closest work is group- and class-robust pruning: DRoP, RCAP, FairCore (ICML 2026) and Jain et al. (NeurIPS 2024). These set group-proportional keep ratios, usually at the sample level. Our quota Q is the batch-level analogue and is already in our ablation; the repair is driven by the floor, not by proportional retention.


Q1. Please See W2a. EquiPrune-F outperforms less aggressive B-PAS at matched savings (+1.54 [+0.19, +2.88]). The gain is not additional training: both use the same batch-epochs, and the difference is that EquiPrune lets the training schedule complete.

Q2. Please See W2c. Use the floor F by default. Q/R are switched on only by a training-time retention check, which selects F in every regime, so no test results are used.

Q3. Please See W4. On 4-grade AMD, where class and race imbalance coexist, the results match the binary task.

Reviewer_kSytOpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
3
Soundness
3(+1)
Read review
Paper summary

The paper audits data pruning for demographic fairness. It runs three pruners (B-PAS, InfoBatch, and EL2N) on six datasets from medical imaging and face analysis. Pruning lowers equity-scaled AUC and worst-group AUC in six of nine training regimes. Group retention logs show that the pruners remove data evenly across groups. The authors therefore attribute the harm to reduced training exposure. Small groups lose the most, and a group scaling model formalizes this. The proposed EquiPrune wraps an existing pruner with three guardrails. A floor stops pruning before too little data remains. A quota keeps each group's retained share close to the overall share. A loss weight boosts groups that fall behind. EquiPrune recovers baseline fairness in most regimes while saving about half the data.

Critical strengths
  1. The mechanism analysis is the strongest part of the paper. Fixed batch membership makes each group's retention exact. Three diagnostics test whether pruning selects against minority-heavy batches, and all three fail (Section 4, Appendix D). Random removal on B-PAS's own schedule is just as harmful (Appendix K). This separates separates which data is removed from how much is removed. That distinction decides which repair applies.

  2. The paper shows that standard fairness metrics miss this harm. Parity metrics report an improvement in most of the harmful cells, because a degraded model compresses its positive rates (Appendix G). Average AUC misses a quarter of them (Appendix C.2). This applies to the fairness evaluation of any efficiency method.

  3. The evaluation is broad and transparently reported. It covers six datasets, several protected attributes, seed-paired differences, and decision rules fixed before the experiments. A sensitivity study estimates its own noise floor (Appendix K). The guardrails also transfer to FairCLIP fine-tuning (Appendix H).

Critical weaknesses
  1. The worst harm comes from running B-PAS outside the range its authors recommend. The threshold schedule here ends forty times higher than the value Alam et al. (2026) recommend for ResNet-50 (Appendix B.3). Their paper reports that milder schedules already stop training around epoch 100. The same collapse appears here. In the worst regime, the training set empties near epoch 100 (Section 4). The sensitivity sweep never reaches the recommended range either (Appendix K). B-PAS also loses about three points of average AUC in that regime (Table 5). This contradicts the audit's premise that pruning preserves average performance. The authors might tune B-PAS to a setting that preserves average AUC, as Alam et al. do, and compare EquiPrune against B-PAS at matched savings.

  2. The per-regime effects are within run-to-run noise. Each cell uses three seeds. The standard error the paper estimates for a three-seed mean is comparable to many entries in Tables 1 and 2 (Appendix K). An independent replication of the worst regime with identical settings shrinks the B-PAS harm to about a fifth of its size. The half-point threshold used for harm and repair sits well inside this noise. Several regime verdicts could flip with new seeds. The pooled dose-response analysis in Appendix K is the most convincing evidence in the paper. The authors ought to lead with it, add seeds for the regimes that carry the claims, and report confidence intervals in the main tables.

  3. The main finding is a known effect. . No pruner harms CheXpert or UTKFace, the two largest datasets (Section 4). The harm concentrates on medical sets of about six thousand training images, where a full training run is already inexpensive. Chen et al. (NeurIPS 2018) attribute part of group disparity to variance that shrinks with group sample size. Rolf et al. (ICML 2021) model each group's risk as a power law in its own sample size and fit it on real data. Equation 1 is a special case of their model, and Proposition 1 follows directly from it. Neither work is cited. The authors could position the audit against these works and test at a scale where pruning saves meaningful compute.

Questions for authors
  1. How was the B-PAS threshold schedule chosen, and what does the audit show at a schedule that preserves average AUC?

  2. With more seeds in the worst regime, does the B-PAS harm settle near the main-campaign value or the replication value?

  3. How does EquiPrune compare with B-PAS tuned to the same data savings without guardrails?

6 comments
AuthorsOpenReview ↗

Response to Reviewer kSyt (1/3)

We thank the reviewer for a careful and constructive review. To address it we ran additional experiments, reported in three new appendix sections of the revised submission:

  • (App. M) B-PAS at its own published thresholds, with a compute-matched comparison;
  • (App. N) five additional seeds with 95% confidence intervals;
  • (App. O) a mechanism analysis of when the harm arises.

If the paper is accepted, we will use the additional page to reorganize the paper based on the discussion. We answer each point below.

Notation. Δ is the seed-paired change against the unpruned baseline, in AUC points ×100. A pair of numbers in square brackets after a value, e.g. −4.84 [−7.68, −2.00], is the 95% confidence interval of that value (a t-interval over seeds); an interval that lies entirely below (above) zero means the change is distinguishable from run-to-run noise. B-PAS threshold schedules are written differently, as "schedule [δ_start, δ_end]", e.g. [5e-6, 5e-5]; these brackets are threshold values, not confidence intervals.


W1. B-PAS runs outside its recommended range; it also loses ~3 AUC points; compare at matched savings.

Our default schedule ([4e-5, 2e-3]) is more aggressive than the ResNet-50 setting Alam et al. report ([5e-6, 5e-5]). However, B-PAS does not have a single recommended δ: the threshold acts on raw activation changes, so its scale depends on the dataset, model and training recipe, and Alam et al. themselves report different schedules for different settings. In practice δ is calibrated per setting, which is cheap (a short pilot run is enough to see how fast batches stabilize). We followed that practice and calibrated δ to reach B-PAS's reported savings range on our data. To show what happens at the published values, (App. M) runs B-PAS at three of its own published schedules on FairVLMed/R50+SGD (5 seeds each):

B-PAS scheduleSavingsΔAUCΔES-AUC
[5e-6, 5e-5] (recommended)~23%−0.73−0.54
[1e-5, 1e-4]~35%+0.03+0.51
[5e-5, 5e-4]~60%−1.96 (p<0.01)−0.63
ours (default)~65%−4.76 (p<0.01)−5.29 [−10.44, −0.14]

At the recommended schedule B-PAS preserves AUC and fairness, but saves only about a quarter of the data. The harm appears at the aggressive end, which Alam et al. themselves describe as "training terminating around epoch 100". That is also what happens here: B-PAS empties its active set and stops training at epoch ~108, with the learning rate still at ~47% of its peak. Across 91 B-PAS runs, the learning rate at the stopping point predicts the fairness loss (Spearman ρ = −0.32, p = 0.002) (App. O). This is the B-PAS operating point a practitioner reaches when targeting the savings B-PAS advertises.

At matched savings, EquiPrune-F (55%) beats B-PAS tuned to ~60%: +1.54 [+0.19, +2.88] ΔES-AUC, while also losing less AUC (−0.77 vs −1.96).

On average AUC, we agree it does not stay flat for B-PAS in this regime. Our point, developed in App. C.2, is that average AUC understates the harm: across the harmful cells, fairness metrics fall more than AUC, and an AUC-only audit misses a quarter of them. We have revised the wording of our first contribution accordingly: it now states that average performance understates the cost of pruning, because subgroup and worst-group performance fall further than average AUC.


W2. Per-regime effects are within run-to-run noise; add seeds and confidence intervals.

We agree that three seeds make single cells noisy. (App. N) adds five seeds (45–49) to FairVLMed/R50+SGD, the regime with the largest effect, and reports 95% confidence intervals. Below, each entry is the mean change (×100) over 8 seeds, with its 95% CI in brackets. An interval that lies entirely below zero means the harm is distinguishable from run-to-run noise; one entirely above zero means the same for the improvement.

FairVLMed/R50+SGD, 8 seedsΔES-AUC [95% CI]Δworst-group AUC [95% CI]
B-PAS vs. unpruned baseline−4.84 [−7.68, −2.00]−5.60 [−8.59, −2.62]
EquiPrune-F vs. B-PAS (same seed)+5.49 [+2.08, +8.89]—
  • The harm is real. B-PAS lowers ES-AUC by 4.84 points; even the most favourable end of the interval is a 2.00-point loss.
  • The repair is real. Adding the floor to the same B-PAS run raises ES-AUC by 5.49 points; the interval's lower end is still +2.08.

Across all regimes, a random-effects meta-analysis gives a pooled B-PAS effect of −1.18 [−2.24, −0.12] ES-AUC (p = 0.029), and all three pruners together give −0.28 [−0.51, −0.04] (p = 0.022). Both intervals exclude zero. Following the reviewer's suggestion, the pooled analysis will lead the results section in the camera-ready.

AuthorsOpenReview ↗

Response to Reviewer kSyt (2/3)

W3. The main finding is a known effect (Chen et al., 2018; Rolf et al., 2021); test at a scale where pruning saves meaningful compute.

We thank the reviewer for these references, which we now cite in the Introduction and Related Work. We agree on the theory. Equation 1 has the functional form of Rolf et al.'s per-group scaling model (their Eq. 4 with τ_g = 0, δ_g = 0 and a shared exponent; it also matches the group learning curves of Chen et al.).

The known effect does not by itself explain our finding, though. Both papers relate a group's risk to the number of distinct samples of that group in the training set. Data pruning does not reduce that number: every pruned batch was trained on for many epochs before it was removed. Equation 1 replaces sample count with exposure, the share of a group's data kept in training per epoch. That substitution is our modelling choice, and neither paper tests it. Our compute-matched control tests it directly: an unpruned run with a shortened schedule has the same exposure as a pruned run at 55% savings, yet shows no fairness loss (below). So neither less data nor less exposure alone produces the harm.

More broadly, our contribution is not only that pruning can hurt small groups, but why. Data pruning is usually treated as a black box: savings and average accuracy are reported, but not what the pruner actually removed or why a group was affected. Our mechanism layer is an attempt to open that box:

  • Retention accounting records, per group and per epoch, how much data each group actually keeps. It shows that the pruners do not select against any group (the retention gap stays below 0.034), and the random-replay control confirms this. So the intuitive explanation, biased selection, is ruled out.
  • The cause is when training ends. An unpruned model trained with a schedule shortened to the same budget (55% savings) shows no fairness loss (−0.15 [−1.03, +0.73]) (App. M). The harm arises because B-PAS empties its active set and stops training before the learning-rate schedule completes (W1) (App. O).

Neither Chen et al. nor Rolf et al. predicts this: that an efficiency method's stopping behaviour, not the amount or selection of data, produces subgroup harm that a compute-matched schedule avoids. EquiPrune's floor is designed from this diagnosis.

On scale: CheXpert and UTKFace are both large and, compared with the medical cohorts, relatively balanced on the attributes we audit (e.g. CheXpert's gender). The null there therefore does not separate size from balance; both point the same way, and both are what the paper predicts (prediction P1). The harm concerns small groups in small, imbalanced cohorts, such as FairVLMed, Glaucoma and AMD. This is exactly where the audit matters: such clinical cohorts are retrained often, and pruning is most attractive to the resource-limited sites that train on them.

AuthorsOpenReview ↗

Response to Reviewer kSyt (3/3)

Q1. How was the B-PAS schedule chosen, and what does the audit show at a schedule that preserves average AUC?

B-PAS's δ is calibrated per dataset and model, because the threshold's scale depends on the data and recipe; this costs only a short pilot run. We calibrated it to reach B-PAS's reported savings range. At the recommended schedule, B-PAS preserves AUC (−0.73) and fairness (−0.54) but saves only ~23% of the data (table in W1; App. M).

Q2. With more seeds in the worst regime, does the harm settle near the main-campaign value or the replication value?

Near the main-campaign value. The five new seeds give −5.29 [−10.44, −0.14], and the main protocol's 8 seeds give −4.84 [−7.68, −2.00]. Pooled over all 14 independent runs of the identical configuration (main, generality, sensitivity and new seeds), ΔES-AUC is −3.40 [−5.28, −1.52] and worst-group AUC −3.82 [−6.12, −1.51] (both p < 0.01). The sensitivity replication (−0.79) was the low outlier (App. N).

Q3. How does EquiPrune compare with B-PAS tuned to the same savings without guardrails?

We ran this comparison directly (App. M). "Tuned" B-PAS means plain B-PAS, no guardrails, run at a milder threshold schedule taken from Alam et al. ([5e-5, 5e-4]), which lands at about the same savings as EquiPrune. Both are run on FairVLMed/R50+SGD with the same five new seeds, and each is paired with the unpruned baseline of the same seed:

Method (no other change)SavingsΔAUCΔES-AUCΔworst-group AUC
B-PAS tuned to matched savings, [5e-5, 5e-4]60%−1.96 (p<0.01)−0.63−0.94
EquiPrune-F (our default schedule + floor)55%−0.77+0.90−0.35

Comparing the two seed by seed, EquiPrune-F is fairer by +1.54 [+0.19, +2.88] ES-AUC points (the interval excludes zero), and it loses about a third as much AUC (−0.77 vs −1.96).

Why tuning alone does not fix B-PAS: a milder schedule only delays the point where B-PAS runs out of batches. At [5e-5, 5e-4] it still stops training early, near epoch 129 on average, with the learning rate at about 31% of its peak (App. O analyses this stopping effect over all B-PAS runs), so it keeps part of the AUC loss. EquiPrune-F keeps a small set of batches until epoch 200, so training finishes its schedule at the same level of savings.

To get B-PAS to preserve AUC without guardrails, the schedule has to be relaxed further, to [1e-5, 1e-4] (ΔAUC +0.03, ΔES-AUC +0.51). That costs savings: it saves 35% of the data, against 55% for EquiPrune-F. So at equal savings EquiPrune-F is fairer than tuned B-PAS, and to match EquiPrune-F's fairness without guardrails, B-PAS gives up about 20 points of savings.

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

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