acceptodds
Under review as a conference paper at ICLR 2027

Rethinking the Evaluation of Training Data Attribution in Generative Models

Abstract

Concerns about the misuse of copyrighted and private data in training image generation models motivate training data attribution (TDA), which assigns each training sample a score measuring its influence on a generated query. TDA methods are commonly evaluated using the Linear Datamodeling Score (LDS), which aggregates attribution scores over sampled subsets to predict changes in model behavior after retraining. However, attribution scores exhibit a long-tailed magnitude distribution, with most scores close to zero. Finite sampling introduces noise into their estimation, and repeated estimates show substantially greater sampling variation relative to the observed score energy in low-influence regions. These fluctuations reflect noise-induced errors in measuring weak influences. Consequently, changing aggregation weights alone can alter LDS without changing the underlying attribution scores, undermining the reliability of method comparisons. For example, restricting the contribution of low-influence regions improves prediction of the full subset responses. Power transformations such as squaring can also improve prediction by suppressing the contribution of low-magnitude scores, giving methods an evaluation advantage without improving their attribution estimates. We propose Signal-to-Noise Ratio LDS (SNR-LDS), which models measurement noise as zero-mean Gaussian and estimates a signal-to-noise ratio for each attribution score. By excluding scores below a common SNR threshold, SNR-LDS limits the contribution of unreliable measurements and aims to reduce the evaluation advantage conferred by reweighting. Deletion experiments on CIFAR-2 Flow Matching models show that removing influencers identified by the method ranked highest by SNR-LDS increases mean query loss more than removing those identified by the method ranked highest by LDS. We further introduce controlled-source retrieval, which directly evaluates source rankings by recovering injected training samples from foreign concepts, complementing SNR-LDS. Code and Data are available at https://anonymous.4open.science/r/SNR-LDS-65B2.

Primary area:
generative models
Keywords:
Training Data Attribution, Generative Model

Reviews

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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_8DzeOpenReview ↗
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3(+1)
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3
Informativeness
3
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1
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Paper summary

This paper revisits the evaluation methodology for training data attribution (TDA) in image generation models such as Flow Matching and diffusion models. It points out that the standard metric, the Linear Datamodeling Score (LDS), can change its value solely through reweighting operations during aggregation, such as excluding low-influence samples or applying squaring and power transformations, without altering the underlying attribution scores at all. This sensitivity arises from the long-tailed distribution of attribution scores and the noise introduced by finite sampling. From this perspective, the paper shows that the reported advantage of DAS may stem not from genuine attribution accuracy but from the suppression of low-influence samples caused by its squaring operation. As a remedy, the paper proposes SNR-LDS, which models measurement noise as zero-mean Gaussian and selects scores using an SNR threshold (ζ=3\zeta=3), and controlled-source retrieval, which directly evaluates attribution rankings by recovering injected samples of foreign concepts. The authors also formulate FMAS, an influence-function-based method for Flow Matching.

Critical strengths
  • The paper clearly demonstrates, with concrete examples, a structural flaw in LDS: its value can shift through aggregation-side reweighting alone, such as truncation of low-influence samples or power and squaring transformations, without any change to the underlying attribution scores. LDS has been used as the de facto standard metric in much prior work, and this flaw directly concerns the reliability of method comparisons themselves. For this reason, the observation is a valuable contribution to the evaluation methodology of the field as a whole.

  • The paper carefully verifies the claim that the reported advantage of DAS arises from the suppression of low-influence samples through squaring rather than from a genuine improvement in attribution accuracy. It does so through controlled comparisons, including applying squaring to other methods and combining it with truncation. In particular, the analysis that compares linear and squared readouts on identical absolute-score heads and shows that the advantage of squaring diminishes as aggregation is restricted to high-influence samples (Fig. 2(c)) provides concrete support for the reweighting explanation. This is a convincing contribution.

Critical weaknesses
  • Although the paper takes "the reliability of evaluation" as its central theme, the proposed evaluator SNR-LDS itself carries a reliability concern. SNR-LDS assumes that the measurement noise follows a zero-mean Gaussian distribution with a single shared scale σq\sigma_q across all samples within each method and query, but the validity of this assumption is not established. As the authors themselves show in Fig. 1(b), sampling variation differs systematically with the magnitude of influence, so the possibility that the noise is sample-dependent cannot be ruled out.

  • A more serious issue is that the paper provides no justification for the choice of the threshold ζ=3\zeta=3. In Fig. 3(a), the authors show that SNR-LDS is robust to reweighting, with changes within 0.39 points. At the same time, the sensitivity analysis in Table 12 shows that the ranking of methods flips as ζ\zeta varies. The central claim of the paper is that LDS is unreliable because it depends on aggregation-side reweighting. However, in exchange for robustness to reweighting, SNR-LDS introduces a dependence along a different axis, namely that its conclusions depend on the choice of the threshold ζ\zeta. This can be read as reproducing, in a different form, the very problem the paper criticizes.

Questions for authors

The following questions all bear on my assessment of the paper.

  1. Regarding the isotropic-variance Gaussian assumption in SNR-LDS, is there any evidence that the score residuals in the central region actually follow a zero-mean Gaussian distribution with homogeneous variance? Is the magnitude-dependent variation shown in Fig. 1(b) consistent with this assumption? If the noise were in fact sample-dependent, to what extent would the validity of the SNR-based selection be undermined?

  2. On what basis was the threshold ζ=3\zeta=3 chosen? Table 12 shows that the ranking of methods reverses depending on ζ\zeta, so is it possible to present a robust conclusion that does not depend on the threshold? Furthermore, how should the robustness to reweighting shown in Fig. 3(a) and the sensitivity to ζ\zeta shown in Table 12 be understood together, from the standpoint of the evaluator's reliability?

4 comments

Thank you for your valuable review and suggestions. Below we try to respond to the comments in Weaknesses (W) and Questions (Q).


W1&Q1: Shared noised scale

To clarify, SNR-LDS does not assume that measurement errors across all samples strictly follow a homoscedastic Gaussian distribution; rather, it uses the zero-mean homoscedastic Gaussian as an approximate central background working model for the near-zero region to locate the boundary where high-influence samples stand out from background error.

First, the central region of the score distribution is dominated by background measurement error. On diffusion models, if the near-zero central region contained Gaussian-distributed true signals, full-sum linear aggregation (vanilla LDS) would be mathematically optimal, and truncating or downweighting the central region via squaring would lose information and lower correlation. However, across all evaluated platforms, excluding or downweighting the near-zero central region substantially improves subset-prediction correlation (Figure 2), confirming that the central bulk contains negligible true attribution signal and is instead dominated by measurement error.

Second, we model this central background error as approximately homoscedastic Gaussian because, for background samples unrelated to a given query, the observed score sums many nearly independent zero-mean fluctuations, which naturally converges to a zero-mean Gaussian in the central region by the central limit theorem (matching the bell-shaped central peak in Figure 1(a)). Moreover, because these unrelated samples have no special gradient alignment with the query, they experience the query's stochastic fluctuations homogeneously and share an approximately uniform scale σ\sigma within the central region.

Furthermore, to test whether noise varies across samples, we independently repeat the four core methods 8 times on CIFAR-2 FM and measure each sample's noise standard deviation sis_i across influence quantiles (normalized by the central-window noise level scs_c):

Method (si/scs_i / s_c)0–50%50–80%80–90%90–95%95–98%98–99%99–100%
FMAS0.991.081.341.652.032.212.77
EK-FAC IF0.981.141.481.802.162.282.62
D-TRAK0.991.031.081.151.231.371.54
DAS1.001.021.071.121.221.351.51

As shown in the table, the sampling noise in the central region is nearly flat across all four methods, supporting our use of a single background scale within the central window.

Finally, although noise increases in the high-influence tail outside the central region, this heteroscedasticity does not undermine SNR-LDS. First, σ^q\hat\sigma_q is fitted only within the central window, where the noise profile is flat. Second, because tail samples have larger noise, accounting for tail heteroscedasticity simply raises their individual thresholds slightly and removes a few borderline samples near the threshold. When we replace the shared sampling variance in σ^q2\hat\sigma_q^2 with each sample's measured variance si2s_i^2 to form a sample-wise noise scale σi\sigma_i at ζ=3\zeta=3, both the SNR-LDS scores and the method ranking remain virtually unchanged:

MetricFMASEK-FAC IFD-TRAKDAS
SNR-LDS (shared scale σ^q\hat\sigma_q)46.5947.4745.1843.05
SNR-LDS (sample-wise scale σi\sigma_i)45.3747.2444.7442.99

We have added this verification to Appendix E.7 (Tables 18 and 19) of the revised paper.

W2&Q2: Threshold ζ\zeta

In Table 12 of the appendix, our goal in examining benchmark performance across ζ\zeta is not to suggest that method rankings arbitrarily flip with ζ\zeta, but to show that when the threshold ζ\zeta is set too low (relaxed), unreliable background noise re-enters aggregation and makes the evaluation untrustworthy.

Specifically, in vanilla LDS, post-hoc reweighting transformations such as squaring suppress the weights of noisy low-influence samples during aggregation, granting artificial performance gains across methods. SNR-LDS addresses this issue by restricting subset aggregation to training samples with reliable attribution predictions. Consequently, ζ\zeta serves as a pre-specified signal-to-noise ratio threshold fixed in the evaluation protocol and applied uniformly across all methods to define what constitutes a reliable prediction.

To determine what signal-to-noise ratio qualifies as reliable, we follow the standard 3σ3\sigma convention in statistics and signal detection, under which pure background noise rarely crosses the threshold. When ζ\zeta is lowered to 11 or 22, a large fraction of the retained set consists of background-noise exceedances, and at ζ=0\zeta = 0, SNR-LDS degenerates completely into vanilla full-sum LDS. Thus, the robustness to reweighting in Figure 3(a) and the sensitivity to small ζ\zeta in Table 12 are two sides of the same mechanism: score reweighting inflates vanilla LDS by suppressing background noise in the ζ<3\zeta < 3 regime; once this unreliable background is filtered out at ζ=3\zeta = 3, reweighting no longer yields artificial gains (Figure 3(a)); conversely, lowering the threshold to ζ≤2\zeta \le 2 in Table 12 re-admits background noise into aggregation, re-exposing the evaluator to reweighting bias and causing the ranking to flip.

To verify this directly, we evaluate how well SNR-LDS at different thresholds ζ\zeta correlates with the counterfactual deletion effect on CIFAR-2 FM. For each query and method, we compare the per-query evaluator score SNR-LDSq(a;ζ)\text{SNR-LDS}_q(a;\zeta) against the true query-loss increase after deleting the method's top-300 or top-1000 training samples and retraining the model:

SNR Threshold ζ\zetaExpected Noise Share in Retained SetCorrelation ρ\rho with Deletion Effect (top-300)Correlation ρ\rho with Deletion Effect (top-1000)
ζ=0\zeta = 0 (vanilla LDS)—0.140.140.070.07
ζ=1\zeta = 188.9%88.9\%0.210.210.160.16
ζ=2\zeta = 240.3%40.3\%0.290.290.290.29
ζ=3\zeta = 3 (default 3σ3\sigma threshold)6.2%6.2\%0.320.320.280.28
ζ=4\zeta = 4<0.5%<0.5\%0.430.430.350.35
ζ=5\zeta = 5<0.1%<0.1\%0.430.430.320.32
ζ=6\zeta = 6<0.1%<0.1\%0.450.450.340.34

As shown in the table, when ζ\zeta is too small (ζ=0,1\zeta=0, 1), the evaluator fails to filter out background noise and correlates poorly with true deletion effects; the ranking flip at ζ=1\zeta=1 in Table 12 is a direct result of this noise contamination. Once ζ\zeta is set high enough to filter out background noise, the correlation with true deletion effects rises substantially and remains stable. Thus, ζ=3\zeta=3 follows the standard 3σ3\sigma convention while lying squarely within the reliable regime where evaluation aligns with true counterfactual effects. We have incorporated these experiments and analyses into Appendix E.2 (Figure 9) of the revised paper.

I thank the authors for their detailed responses and the additional experiments. My two main concerns have been addressed.

On the Gaussian background assumption (W1/Q1), the new results in Appendix E.7 (Tables 18 and 19) showing near-homogeneous central noise and a stable ranking under sample-wise scales resolve my concern.

On the threshold ζ=3\zeta = 3 (W2/Q2), the reframing of the Table 12 behavior as background noise re-entering aggregation, together with Figure 9 showing that ζ=3\zeta = 3 follows the 3σ3\sigma convention while aligning with counterfactual deletion effects, answers my concern that SNR-LDS might reproduce the reweighting dependence of LDS.

I am raising my rating from 2 to 3.

Dear Reviewer, Thank you very much for engaging with our response and raising your score.

Reviewer_TR6AOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
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Soundness
2
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Paper summary

This paper studies the sensitivity of the Linear Datamodeling Score (LDS) to noise and transformations of attribution scores. The authors propose SNR-LDS, which estimates a noise scale from the central score distribution and removes scores below a common threshold before aggregation. They also introduce a controlled-source retrieval task using injected concepts and an influence-function method for flow matching, FMAS. The experiments cover CIFAR and ArtBench, with repeated score estimation and deletion-and-retraining results to assess the proposed evaluation.

Critical strengths
  1. The observation that score transformations can substantially change method rankings is interesting. Applying these transformations to fixed scores makes the effect easier to examine.

  2. The authors evaluate actual deletion effects as well as source retrieval. This is useful for checking whether conclusions drawn from LDS have consequences beyond the metric itself.

  3. The selection rule does not use the measured subset responses, and the paper reports threshold sensitivity and failed fits. These details are important for assessing the proposed evaluator.

Critical weaknesses
  1. It is unclear to me why the central score distribution provides an estimate of sampling noise. Section 4.1 measures variation across repeated estimates of the same score, while Section 4.3 fits a distribution across different training examples in one run. The latter includes real differences in influence, even if those influences are small. Since repeated estimates are already available, could the authors compare the fitted noise scale directly with the observed residuals? Its dependence on the sampling budget would also be a useful check.

  2. The reweighting experiment in Figure 3(a) fixes the mask obtained from the original scores. Does the result still hold if noise fitting and selection are repeated after each transformation? Appendix D.1 also requires DAS's signed scores before squaring, which are unavailable from the final squared scores alone. The paper should make clear what information the evaluator requires and whether its robustness depends on access to these intermediate scores.

  3. Failed fits are a substantial issue: Appendix E.4 reports 7,354 failures out of 24,400 query records, including all pixel/CLIP fits. Tables 1 and 11 then average each method over its own valid queries. How can these averages be fairly compared when the query sets differ? The shared-query intersection used for the evaluator-selected deletion experiment is appropriate, but the main benchmark tables need the same treatment, along with an account of the excluded queries.

  4. More evidence is needed for the claim that SNR-LDS is a better attribution evaluator. Better subset-loss prediction after reweighting can itself be a useful improvement; a change in LDS is not sufficient to show that LDS is misleading. The deletion comparison supports the authors' argument, but uses 50 queries from one CIFAR-2 model seed. I would like to see whether SNR-LDS agrees better with deletion effects across other settings, and whether simpler thresholding or shrinkage methods obtain similar results.

Questions for authors

see Critical Weaknesses

4 comments

Thank you for your valuable review and suggestions. Below we respond point by point to the comments in Weaknesses (W) and Questions (Q).

W1: Noise Estimation

The two quantities measure different components linked by a variance decomposition: the repeat residual ss (Section 4.1) is a single sample's score standard deviation across repeated runs, whereas the fitted scale σ^\hat\sigma (Section 4.3) is the central distribution width across training samples within one run. For central samples, σ^2≈s2+V\hat\sigma^2 \approx s^2 + V, where VV is the across-sample variance of expected scores that remains invariant across repeats.

On CIFAR-2 FM (16 generation and 16 validation queries, RMS-normalized), repeating D-TRAK and FMAS 16 times gives the central repeat residual ss, single-run fitted scale σ^1\hat\sigma_1, and 16-run averaged scale σ^16\hat\sigma_{16}:

Metric (mean across queries)D-TRAK genD-TRAK valFMAS genFMAS val
Repeated-sampling noise scale ss0.180.170.220.24
Single-run fitted scale σ^1\hat\sigma_10.640.610.830.69
16×16\times-run fitted scale σ^16\hat\sigma_{16}0.620.590.840.65

Increasing the sampling budget barely changes σ^\hat\sigma, which remains larger than ss due to the non-sampling variance VV. We test from two angles whether VV reflects genuine influence.

First, genuine influence depends only on the data and model, so differently constructed methods should rank central samples consistently if VV reflected weak true influence. On the 16-run averaged scores, we compare the across-sample Spearman correlation between FMAS and D-TRAK with each method's split-half correlation (first 8 runs versus last 8 runs):

Spearman Rank Correlation (16-run average)genval
High-SNR samples (ζ=3\zeta=3)0.350.27
Central samples0.010.05
Central samples, split-half within method (8 vs. 8 runs)0.96 / 0.970.94 / 0.97

Note: Central samples are the intersection of both methods' central fitting windows (~45% of samples); high-SNR samples satisfy ∣t∣>3σ^|t|>3\hat\sigma under either method.

Within each method, split-half correlation is near unity, confirming that sampling noise is averaged out and central rankings reflect a reproducible deterministic component VV. Across methods, however, FMAS and D-TRAK correlate positively on high-SNR samples yet are uncorrelated (0.010.01–0.050.05) on central samples, showing that VV stems predominantly from construction-dependent method approximation error rather than genuine influence. Pairwise comparisons across all four core methods and three model seeds confirm the same pattern: central scores correlate only within shared constructions (0.670.67 for FMAS–EK-FAC IF; 0.350.35 for D-TRAK–DAS), dropping to 0.030.03–0.040.04 across constructions while remaining 0.280.28–0.340.34 on high-SNR samples.

Second, we test directly on retrained subsets whether central scores carry predictive signal once sampling noise is averaged out:

Aggregation Scheme (LDS ×100\times 100)D-TRAK genD-TRAK valFMAS genFMAS val
All samples41.144.737.946.1
Central samples only2.65.01.61.7
Central samples only (16-run average)3.15.52.23.7
High-SNR samples only (ζ=3\zeta=3)47.048.646.852.3
High-SNR + 16-run averaged central samples44.147.241.048.3

Even after 16-run averaging, central samples alone yield near-zero LDS, and adding them back to high-SNR samples degrades LDS in every setting. Thus, VV is dominated by method error rather than weak genuine influence, and σ^\hat\sigma captures the combined background error scale (sampling noise plus method error) that a single-run score must exceed to be reliable. We have clarified this interpretation of σ^\hat\sigma in Section 4.3 of the revised paper and will include these repeat experiments in the appendix.

W2: Input of SNR-LDS

The background modeling of SNR-LDS builds on the natural semantics of attribution scores, where 00 denotes no influence and positive or negative signs indicate the direction of influence. It fits a zero-mean Gaussian distribution in the central region around 00 to estimate the background error scale σ^q\hat\sigma_q.

Like D-TRAK, DAS is built on a signed projected-gradient inner product, but it applies squaring in its final step so that its output becomes non-negative, retaining only magnitude ("absolute influence") without directional sign and shifting the distribution center away from 00; consequently, a zero-mean Gaussian cannot be fitted directly on the squared scores. To handle this, we treat sample selection and aggregation readout separately: we fit σ^q\hat\sigma_q and perform SNR selection on DAS's pre-square signed inner-product scores tqit_{qi}, while keeping DAS's native squared scores tqi2t_{qi}^2 unchanged during subset summation (Appendix D.1). Because squaring is strictly monotonic in magnitude, ∣tqi∣>ζσ^q|t_{qi}|>\zeta\hat\sigma_q and tqi2>ζ2σ^q2t_{qi}^2>\zeta^2\hat\sigma_q^2 select the exact same set of samples; moreover, on pre-square signed scores, DAS exhibits distributional properties closely aligned with D-TRAK, which shares its projected-gradient construction. For the same reason, in the reweighting experiment of Figure 3(a), the background scale cannot be refitted after a terminal power transformation. On CIFAR-2 FM generation queries (three model seeds), we compare fitting and selecting on the original signed scores against refitting and selecting on the transformed scores:

Readout and Selection (SNR-LDS ×100\times 100)FMASEK-FAC IFD-TRAKDAS
Linear readout, selection fitted on signed scores44.5443.3144.5043.72
Squared readout, same selection44.8542.8144.4043.73
Sign-preserving squared readout, same selection46.1645.0144.3943.81
Squared readout, selection refitted on squared scores49.8046.7946.8146.44
Sign-preserving squared readout, selection refitted on transformed scores50.1247.9945.8145.24
Retained fraction: signed fit / squared refit / sign-preserving squared refit3.9% / 25.0% / 32.9%4.5% / 25.7% / 33.6%5.1% / 26.1% / 33.9%4.9% / 25.9% / 33.8%

When selection is completed on the original signed scores, changing the terminal readout affects SNR-LDS by at most 0.50.5 points (ordinary squaring) and 1.71.7 points (sign-preserving squaring), far smaller than the 8.18.1–11.711.7 point swings under full-sum LDS (Table 4). Once refitted on the transformed scores, however, regardless of whether the transformation preserves the sign, the retained fraction inflates from roughly 5%5\% to 25%25\%–34%34\%, and SNR-LDS rises simultaneously by 1.31.3–5.65.6 points across all four methods. This happens because a nonlinear power transformation with exponent p>1p>1 (whether ∣t∣p|t|^p or sign⁡(t)∣t∣p\operatorname{sign}(t)|t|^p) strongly compresses small-magnitude scores near 00 toward 00, artificially narrowing the central region relative to the tails and violating the additive zero-mean Gaussian background assumption; refitting under this distortion severely underestimates the background scale and re-admits a large number of background samples into aggregation.

Therefore, the robustness of SNR-LDS indeed requires signed scores without terminal nonlinear compression where 00 denotes no influence (for mainstream gradient-based attribution methods, this is directly the output of their core bilinear inner product). For settings that output only non-negative similarities (such as pixel and CLIP similarities; see W3) or provide access only to black-box nonlinearly transformed scores, Controlled-Source Retrieval proposed in Section 4.4—which depends solely on sample rankings and is completely invariant to monotonic reweighting—provides a complementary evaluation. We have explicitly clarified this input requirement and scope of applicability, along with the refitting comparison above, in Section 4.3 and Appendix D.1 of the revised paper.

W3: Failed Fits

We agree with this comment and have updated the main benchmark tables (Tables 1 and 11) in the revised paper to report all methods on the Shared-Query Intersection, while removing pure image-similarity baselines (Raw pixel and CLIP similarity) from the main attribution tables.

Regarding the sources of failed fits in Appendix E.4:

  1. Most failed fits come from the pixel and CLIP similarity baselines, which measure feature similarity rather than counterfactual retraining effects; their score distributions lie far from 00, making SNR-LDS inapplicable to them by definition.
  2. Among gradient-based attribution methods, Relative IF, Renormalized IF, TRAK, D-TRAK, and DAS have zero failed fits across all platforms. The remaining failures occur when a method assigns predominantly same-signed scores on a query, shifting the distribution peak away from 00; these come mainly from unpreconditioned raw-trajectory baselines (TracInCP, GAS, Grad-Cos, and Journey-TRAK), with only a few cases in FMAS and EK-FAC IF on CIFAR-2 FM (and zero on ArtBench-2 and CIFAR-2 DDPM).

The recalculated results on the Shared-Query Intersection across the 8 core attribution methods are shown below (headers list shared query counts, and parentheses show differences from the original table):

MethodC2 FM Val (70–77 q)C2 FM Gen (75–82 q)C2 DDPM Val (90 q)C2 DDPM Gen (96 q)AB2 Val (100 q)AB2 Gen (100 q)C10 FM Val (91–94 q)C10 FM Gen (93–98 q)
Grad-Dot1.90±1.451.90\pm1.45 (+0.05)1.34±1.081.34\pm1.08 (-0.39)0.040.04 (+0.00)−0.18-0.18 (+0.00)21.4621.46 (+0.00)15.5215.52 (+0.00)0.89±0.650.89\pm0.65 (+0.05)−0.43±0.83-0.43\pm0.83 (-0.06)
Relative IF32.81±0.2532.81\pm0.25 (+0.03)24.44±0.4724.44\pm0.47 (+1.64)32.8232.82 (-0.89)22.9822.98 (+0.22)26.8126.81 (+0.00)19.7119.71 (+0.00)27.57±1.0227.57\pm1.02 (+0.50)21.11±1.4821.11\pm1.48 (-0.13)
Renormalized IF31.18±0.9031.18\pm0.90 (-0.16)23.41±1.3323.41\pm1.33 (+1.18)25.9325.93 (-0.43)16.3516.35 (+0.21)27.0027.00 (+0.00)18.1318.13 (+0.00)22.45±0.5422.45\pm0.54 (+0.14)16.03±1.2916.03\pm1.29 (+0.28)
TRAK31.87±0.7631.87\pm0.76 (-0.11)22.51±1.3622.51\pm1.36 (+0.88)32.8532.85 (-0.91)21.3321.33 (+0.16)26.4926.49 (+0.00)17.0717.07 (+0.00)25.52±0.9925.52\pm0.99 (+0.16)18.81±1.5818.81\pm1.58 (-0.03)
D-TRAK47.46±0.8847.46\pm0.88 (-1.58)44.18±1.7744.18\pm1.77 (-0.31)38.8238.82 (-0.58)30.5530.55 (+0.17)36.3136.31 (+0.00)30.0130.01 (+0.00)38.62±1.0938.62\pm1.09 (+0.44)35.30±1.1235.30\pm1.12 (-0.37)
DAS49.26±0.7349.26\pm0.73 (-1.19)42.99±2.0342.99\pm2.03 (-0.75)40.5940.59 (-0.60)31.2331.23 (+0.20)38.48\mathbf{38.48} (+0.00)30.91\mathbf{30.91} (+0.00)44.21±0.69\mathbf{44.21\pm0.69} (+0.13)40.02±0.59\mathbf{40.02\pm0.59} (-0.48)
EK-FAC IF48.88±1.8348.88\pm1.83 (-0.03)43.36±3.0443.36\pm3.04 (+0.05)43.4043.40 (-0.60)35.1235.12 (+0.43)30.3930.39 (+0.00)20.2720.27 (+0.00)35.77±0.9535.77\pm0.95 (-0.11)32.73±0.4132.73\pm0.41 (-0.25)
FMAS49.62±1.02\mathbf{49.62\pm1.02} (+0.01)44.95±1.65\mathbf{44.95\pm1.65} (+0.41)43.62\mathbf{43.62} (-0.47)35.49\mathbf{35.49} (+0.55)27.7527.75 (+0.00)19.6719.67 (+0.00)37.89±0.4737.89\pm0.47 (-0.04)35.56±0.8835.56\pm0.88 (+0.00)

The shared-query scores are nearly identical to the original tables, leaving all winning methods and conclusions unchanged; we have adopted this shared-query table in the main text and detailed the excluded queries in Appendix E.4.

W4: Correlation to Counterfactual Deletion

We conducted three experiments examining why reweighting gains do not stem from per-sample magnitude calibration, how SNR-LDS relates to simpler truncation or squaring baselines, and whether SNR-LDS aligns better with deletion effects on two additional platforms.

First, if squaring improved subset prediction by calibrating per-sample magnitudes, squared readouts should consistently beat linear readouts within each magnitude band. Under the Figure 2(c) setup, we compare Linear (τ\tau), Signed-Squared (sign⁡(τ)τ2\operatorname{sign}(\tau)\tau^2), Squared (τ2\tau^2), and an attribution-free baseline Const = 1 (setting all in-band scores to 11 to count only how many in-band samples are deleted):

FMAS Readout (LDS ×100\times 100)0–5%5–20%20–50%50–100%Full 0–100%
Linear (τ\tau)47.8811.043.40−1.4039.37
Signed-Squared (sign⁡(τ)τ2\operatorname{sign}(\tau)\tau^2)49.88 (+2.00)11.74 (+0.69)3.37 (−0.03)−1.10 (+0.30)50.54 (+11.17)
Squared (τ2\tau^2)48.62 (+0.74)12.63 (+1.59)9.09 (+5.69)6.89 (+8.29)51.09 (+11.72)
Const = 1 (in-band scores set to 1)37.5612.048.9810.5924.15

Note: Parentheses show differences from Linear; EK-FAC IF, D-TRAK, and DAS show the same pattern.

Signed-Squared gives negligible gain within individual bands and jumps only under 0–100% full summation by compressing noisy tail scores that otherwise dilute the 0–5% head. Meanwhile, ordinary Squared in 5–100% is matched or exceeded by Const = 1 simply because deleting more samples raises retraining loss. Both effects arise at aggregation without improving per-sample rankings and apply post-hoc to any method (Table 4), so full-sum LDS conflates this readout artifact with attribution quality.

Second, on CIFAR-2 FM, we compare the Spearman ρ\rho of five evaluators with counterfactual deletion effects (query-loss increase after deleting each method's top-300 or top-1000 samples and retraining) on the 50-query deletion panel across the 43 shared valid queries and 4 methods (172 pairs; scatter plots in Figure 8, Appendix D.4):

Deletion BudgetVanilla LDSFixed Top-20%Fixed Top-5%Uniform SquareSNR-LDS (ζ=3\zeta=3)
top-3000.140.210.360.280.32
top-10000.070.160.360.260.28

SNR-LDS improves over vanilla LDS by +0.18 [0.08,0.28]+0.18\,[0.08, 0.28] and +0.21 [0.10,0.32]+0.21\,[0.10, 0.32] (95% query bootstrap CIs). Fixed top-5%, uniform squaring, and SNR-LDS reach comparable alignment (fixed top-5% slightly higher) and all substantially beat vanilla LDS, corroborating one another as different realizations of the same mechanism. Both fixed-fraction truncation and SNR selection keep top-∣τ∣|\tau| samples, differing only in how head size is set: on CIFAR-2 FM, ζ=3\zeta=3 retains 4%–5% on average (matching top-5%), and aligning both by retained fraction places their correlations onto nearly the same curve:

Retained FractionSNR Selectionρ\rho (top-300 / top-1000)Fixed Fractionρ\rho (top-300 / top-1000)
~20%ζ=1.5\zeta=1.50.25 / 0.23top-20%0.21 / 0.16
~10%ζ=2\zeta=20.29 / 0.29top-10%0.29 / 0.29
~5%ζ=3\zeta=30.32 / 0.28top-5%0.36 / 0.36
~2%ζ=4\zeta=40.43 / 0.35top-2%0.42 / 0.38

As noted in Section 4.2, alignment with deletion effects depends on restricting aggregation to the reliable head whether defined by a fixed fraction or an SNR threshold, making both complementary in practice. Fixed-fraction truncation requires no fitting and serves as a fitting-free reference at a matched head size, though its fraction must be pre-specified (on CIFAR-2 FM, 5% works well whereas 20% degrades nearly back to vanilla LDS). SNR-LDS determines the head size directly from the score distribution under a pre-fixed threshold, yielding ~5% on CIFAR-2 FM while adapting across settings; uniform squaring achieves a similar effect by altering native readouts.

Third, we repeated top-300 deletion and retraining for FMAS and DAS across 50 generation queries (100 pairs) on ArtBench-2 (SD3.5) and CIFAR-2 DDPM, measuring Spearman ρ\rho between evaluator scores and query-loss increases:

Platform (top-300 deletion)Vanilla LDSSNR-LDS (ζ=3\zeta=3)
CIFAR-2 FM0.140.32
CIFAR-2 DDPM0.210.39
ArtBench-2 (SD3.5)0.260.40

On both additional platforms, while vanilla LDS already correlates positively with deletion effects, SNR-LDS correlates substantially better. All diagnostics, baseline comparisons, and cross-platform deletion experiments above are included in Appendix D.4 (Figure 8) of the revised paper.

Reviewer_24oHOpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper focuses on improving one of the commonly used metrics for training data attribution--Linear Data Modeling Score (LDS). LDS is a metric that aggregates per-training-point attribution scores linearly on a random subset to see whether the aggregated score predicts the testing loss of the model trained on the same random subset. The paper argues that attribution scores are noisy, and it introduces a signal-to-noise ratio LDS that instead only aggregates attribution scores if they pass a certain noise threshold. The experiments are mainly carried out in a diffusion model attribution setting, where the most favored method from SNR-LDS out of some selected methods yields the strongest deletion counterfactual effect.

Critical strengths
  1. I agree that attribution methods have a noise problem in general, and I appreciate the analysis to characterize this behavior.
Critical weaknesses

I have several major concerns about this paper that I wish the authors could help clarify. Currently, these concerns lead to my weak-reject ratings.

  1. Is it fair, as an evaluation metric, to "correct" the noise introduced by a method? While I understand that most current attribution algorithms are noisy, it doesn't mean that future attribution methods won't correct this behavior. And this metric will lead to an unfair comparison in that regard.
  2. Since the paper is proposing a change in the evaluation metric, it should study whether the metric still works on other generative modelling setups like language modelling.
  3. Instead of showing tables, it will be great to show plots of SNR-LDS vs counterfactual performance (e.g., deletion) and compare it with LDS vs counterfactual. The motivation for this is to get a clearer sense of the correlation between them, and ideally SNR-LDS will have a better correlation than plain LDS.
Questions for authors

It is unclear what this evaluation implies for algorithms. For example, one application of attribution is to identify influential training images that are responsible for a given output. If following the "suggested fix", where we ignore any training images where the attribution score didn't pass the noise threshold, we might discard ones that are actually influential. Another way to read this paper is that the ones with noisy attribution scores are usually the low-influence ones that we don't usually care about, but the LDS score still includes them because it is designed to aggregate random subsets. In that case, I would be more convinced about the metric.

2 comments

Thank you for your valuable review and suggestions. Below we try to respond to the comments in Weaknesses (W) and Questions (Q).


W1 & Q1: Fairness and Implications for Algorithms

We agree with your interpretation in Q1: samples with noisy attribution scores are usually the low-influence ones that downstream tasks do not care about, yet vanilla LDS still includes them because it aggregates random subsets, which in turn creates the vulnerability to post-hoc score reweighting. Accordingly, SNR-LDS modifies only the evaluator's aggregation protocol when predicting random-subset retraining outcomes; it neither asks attribution algorithms to discard sub-threshold images in downstream applications nor "corrects" or excuses errors for high-noise methods at the expense of future low-noise algorithms.

Crucially, SNR-LDS restricts aggregation only on the predicted score side, while the ground-truth retraining response is still measured over the full subset without any truncation. Because the ground-truth response retains the counterfactual effects of all samples in the subset, this creates a direct reward-and-penalty mechanism:

  • When a method is more accurate (lower noise), its fitted σ^q\hat\sigma_q is smaller, allowing more genuine moderate- and weak-influence signals to pass the threshold and enter aggregation alongside more accurate head signals, which recovers the subset loss changes more completely and yields a higher SNR-LDS.
  • Conversely, when a method is noisier or assigns a low score to a genuinely influential sample so that it fails to pass the 3σ^q3\hat\sigma_q threshold, that sample's true effect still remains in the ground-truth response; omitting it from the predicted sum causes a mismatch with the ground truth and directly penalizes the method's SNR-LDS.

Empirically, we verify that SNR-LDS rewards lower-noise methods on CIFAR-2 FM using FMAS (Appendix C.3). When we increase the Monte Carlo sampling budget by 16×16\times to reduce sampling noise and improve attribution accuracy, SNR-LDS reflects the accuracy improvement even more clearly than vanilla LDS:

EvaluatorGeneration Gain (16×16\times Budget)Validation Gain (16×16\times Budget)
Vanilla LDS+1.8+0.5
SNR-LDS+3.8+4.0

In Appendix A.5, we provide a mathematical analysis characterizing the distributions of influence signals and prediction noise in image generative models, formalizing why fitting σ^q\hat\sigma_q rewards accurate methods while penalizing noisy ones. Furthermore, for the downstream goal of identifying training images responsible for a given output, we also include Controlled-Source Retrieval (Section 5.4), which evaluates source identification directly without subset aggregation. We will revise the Introduction and Section 4.3 to foreground this interpretation and eliminate any ambiguity.


W3: Correlation to counterfactual deletion

To directly compare how well SNR-LDS and vanilla LDS align with counterfactual performance, we compare per-query evaluator scores against counterfactual deletion effects across the four core methods (FMAS, EK-FAC IF, D-TRAK, and DAS) on CIFAR-2 FM. Specifically, for each query and method, we pair the evaluator's score (horizontal axis) with the true query-loss increase after deleting the method's top-300 or top-1000 training samples and retraining the model (vertical axis). The correlations between the evaluator scores and counterfactual deletion effects for vanilla LDS and SNR-LDS (ζ=3\zeta=3) under both deletion budgets are summarized below (scatter plots are provided in Figure 7 of Appendix D.3 in the revised paper):

Deletion BudgetLDS ρ\rhoSNR-LDS (ζ=3\zeta=3) ρ\rho
top-3000.140.32
top-10000.070.28

As shown in the table and the scatter plots in Figure 7 of Appendix D.3 in the revised paper, vanilla LDS (left column) correlates poorly with the counterfactual deletion effect. It assigns high evaluation scores to DAS (yellow), even though its actual deletion loss increases lie near the bottom, while assigning lower scores to FMAS (blue) and EK-FAC IF (orange), which achieve much stronger deletion effects. In contrast, SNR-LDS (right column) aligns much better with the counterfactual deletion effect. Once low-SNR background samples are excluded from aggregation, methods with stronger deletion effects (FMAS and EK-FAC IF) shift to the right and DAS shifts to the left, forming a clear positive trend.

W2: Language Model

We conducted the same diagnostic and evaluation experiments on the WikiText-2 / GPT-2 language modeling benchmark from dattri [1], evaluating 12 configurations across 8 attribution methods alongside a random baseline.

First, we examine the per-query normalized score distributions across training samples (shown in Figure 12 of Appendix E.6 in the revised paper). Except for the EK-FAC IF family, which shows a relatively sharp peak, the score distributions of most methods closely resemble a Gaussian distribution (similar to Random).

Second, we evaluate LDS (×100\times 100) within disjoint magnitude bands using linear (τ\tau) or squared (τ2\tau^2) readouts for two representative methods:

Method0–5%5–20%20–50%50–100%Full Aggregation
EK-FAC IF37.2511.417.074.3738.41
EK-FAC IF2^232.361.92−2.58−3.1632.80
TRAK-5024.7210.788.274.2126.52
TRAK-502^223.182.07−1.01−2.3623.16

Unlike in diffusion models, all configurations maintain positive LDS across the 5–20%, 20–50%, and 50–100% bands, showing that moderate- and low-magnitude regions carry genuine predictive signal. Consequently, truncating to 0–5% lowers LDS relative to full aggregation, and squaring (τ2\tau^2) further degrades performance by discarding sign information and suppressing these informative low-magnitude scores.

Third, the benchmark results (LDS ×100\times 100) across all 12 configurations under vanilla LDS and SNR-LDS (ζ=3\zeta=3) are summarized below:

MethodVanilla LDSSNR-LDS (ζ=3\zeta=3)Δ(SNR-LDS−LDS)\Delta(\text{SNR-LDS} - \text{LDS})Retained Fraction at ζ=3\zeta=3 (%)
EK-FAC IF + RelatIF38.6135.95−2.653.2
EK-FAC IF38.4136.02−2.393.1
TRAK-5026.5223.57−2.951.3
TRAK-1022.1620.51−1.650.8
dropout-TRAK-1020.6017.79−2.810.6
TRAK-518.5617.32−1.240.5
dropout-TRAK-516.9514.02−2.920.4
FactGraSS16.9119.81+2.900.7
LoGra16.8519.67+2.820.6
TRAK-19.516.75−2.760.3
Grad-Dot6.123.07−3.050.3
Grad-Cos6.083.36−2.720.1
Random−0.31−0.80−0.500.3

Overall, SNR-LDS and vanilla LDS yield highly consistent rankings and select the same top-performing family (EK-FAC IF). Only FactGraSS and LoGra—which incur larger low-rank projection errors—improve after filtering out the low-SNR background, whereas the remaining configurations dip slightly because their moderate- and low-magnitude bands retain positive signal.

These results reveal a fundamental difference in influence distributions between diffusion models and autoregressive language models, driven by how many training samples govern a query's loss. In diffusion models, the optimal denoiser weights training images by ∝exp⁡(−∥xt−αtxi∥2/2σt2)\propto \exp(-\|x_t-\alpha_t x_i\|^2/2\sigma_t^2), which decays exponentially with distance; influence concentrates on a few nearest neighbors in a sparse heavy-tailed distribution, leaving distant samples with near-zero true effect. In autoregressive language models, a query's loss sums hundreds of next-token predictions that rely on frequent words, punctuation, and syntactic patterns shared across the corpus, spreading small but genuine counterfactual effects in a dense distribution across almost all training chunks.

This contrast corroborates our theoretical analysis in Appendix A.5 from the opposite regime. When true influence is sparse and low-magnitude regions are dominated by estimation noise (as in diffusion and flow matching), full-sum LDS is vulnerable to reweighting and SNR-LDS is essential for reliable evaluation; when influence is dense (as in autoregressive language modeling), full-sum aggregation already works well, while SNR-LDS preserves method rankings and still filters background noise for coarser approximations (LoGra, FactGraSS). These experiments and the cross-paradigm analysis are included in Appendix E.6 of the revised paper (Figure 12 and Tables 16–17).

References:

[1] Deng et al., dattri: A Library for Efficient Data Attribution, NeurIPS 2024.
[2] Grosse et al., Studying Large Language Model Generalization with Influence Functions, arXiv:2308.03296.
[3] Choe et al., What is Your Data Worth to GPT? LLM-Scale Data Valuation with Influence Functions, arXiv:2405.13954.
[4] Hu et al., GraSS: Scalable Data Attribution with Gradient Sparsification and Sparse Projection, NeurIPS 2025.
[5] Deng et al., Efficient Ensembles Improve Training Data Attribution, arXiv:2405.17293.

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