acceptodds
Under review as a conference paper at ICLR 2027

Which Influence Are We Estimating? The Role of Counterfactual Specifications in Data Attribution

Abstract

Estimating the influence of training examples on model behavior is essential for data debugging, valuation, and attribution. Existing influence estimators often produce incompatible rankings, which are commonly ascribed to approximation error. We argue that a more fundamental source of disagreement is specification mismatch: influence depends on the behavior being attributed, the intervention applied to each training example, and the counterfactual training process that maps the intervention to a model response. These choices are especially important when the target behavior requires a tractable surrogate, such as query loss, a logit, or a margin. We formalize influence as a counterfactual estimand, distinguish specification mismatch across estimands from approximation error in estimating a fixed estimand, and organize representative estimators by their implied specifications. We further derive a local decomposition that exposes how behavior signals, training signals, and counterfactual parameter responses interact. Controlled experiments show that exact estimands under different specifications can induce different rankings, whereas approximation error grows as perturbations move farther from their linearization points. Experiments on noisy label detection and LLM attribution show that specification choices significantly affect attribution quality, especially for the choice of behavior surrogate. Behavior-aligned specifications can identify target-specific training examples obscured by default loss-based or similarity-based specifications. These results establish specification analysis as a necessary first step for interpreting and comparing data influence estimators.

Primary area:
interpretability and explainable AI
Keywords:
Training data attribution, Influence function, Large language models

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_csRxOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper argues that disagreement between data attribution methods can come from asking different counterfactual questions, rather than simply estimating the same quantity with different levels of accuracy. It describes an influence specification through three components: the behavior being measured, the intervention on a training example, and the counterfactual training process. It also presents a local decomposition that separates the behavior signal, training signal, and parameter response. The experiments first study specification changes and approximation error in controlled settings, then examine noisy-label detection and LLM attribution. The main practical finding is that the best behavior surrogate depends on both the attribution method and the task. The paper supports this finding with experiments across several architectures and LLMs, including removal-and-retraining tests.

Critical strengths

The experiments go beyond showing that different methods produce different rankings. The controlled comparisons separate changes in the target quantity from errors in approximating a fixed target. The practical experiments then show why this distinction matters. For example, on CIFAR-10 at 20% label noise, changing from trusted loss to target logit improves TracIn’s AUPRC from 0.349 to 0.602, but reduces LiSSA’s AUPRC from 0.535 to 0.421. This is a useful result because it challenges the idea that there is one behavior surrogate that should work best across estimators.

The removal-and-retraining results give the practical claims more weight. In Table 17, removing the top 10% of examples selected by TracIn with answer logit reduces Qwen3-8B’s backdoor attack success rate from 0.809 to 0.053, close to 0.050 after oracle poison removal, with little change in clean accuracy. The benign-trigger controls also make this more informative than simply detecting a shared trigger string. I appreciate that the appendix includes additional LLMs and signal-augmented similarity baselines, which help qualify the main comparisons.

Critical weaknesses

The distinction between specifications and approximations needs more consistency. Section 4 describes an “exact” comparison involving a damped inverse-Hessian response, but it is unclear whether this represents a derivative, a constructed local update, or a finite re-optimization effect. This distinction is central to the paper. Proposition 1 also needs a scope restriction: its proof applies to deterministic outcomes, while Equation (1) allows stochastic outcomes whose expected rankings need not survive a nonlinear monotone transformation.

The practical comparisons need clearer implementation details and a tighter control. Appendix A.2 does not fully specify the LLM implementations of TRAK and LESS, including checkpoints, normalization, and query aggregation, making it hard to verify what stays fixed across surrogates. An answer-token loss or log-probability baseline would also help: moving from full-response loss to answer logit changes both the token span and the readout, so the current results do not separate their contributions.

Questions for authors

What exactly is the inverse-Hessian estimand in the training-process comparison? Please specify the counterfactual process, the role of damping, and whether the reported quantity is a derivative or a finite behavior change. For the removal-versus-upweighting comparison, please also give the objective normalization and sign alignment explicitly, since the two interventions act in opposite directions.

Can Proposition 1 be restricted to deterministic counterfactuals, or extended under appropriate assumptions for the expected estimand in Equation (1)? The remark about first-order approximations also needs qualification: at a common factual point, a differentiable increasing transformation with positive derivative simply rescales the behavior gradient for a fixed query, so it does not by itself change the first-order ranking.

How were TRAK and LESS adapted to each behavior surrogate? Please specify the training-side quantities, optimizer treatment, normalization, checkpoints, and aggregation over queries. For answer-token readouts, is the preceding rationale teacher-forced or generated? An answer-only negative log-likelihood baseline would help interpret the response-corruption results.

Could you sharpen the distinction from Bae et al. (2022)? That work already argues that influence estimates can approximate a different counterfactual object, the proximal Bregman response function, rather than leave-one-out retraining. Appendix D acknowledges the paper, but describes its contribution too narrowly as an infinitesimal-upweighting versus removal distinction. I see the behavior-surrogate experiments as the clearest additional contribution here, and would encourage the authors to position the paper around that extension. See Bae et al. (2022).

2 comments
AuthorsOpenReview ↗

Response to Reviewer csRx (1/2)

Thank you for your thoughtful review and constructive suggestions. We appreciate your recognition of our controlled experiments separating specification mismatch from approximation error, and we are glad you found the interactions between estimators and behavior surrogates informative and the removal-and-retraining results supportive of our practical claims. Below are our responses to the issues raised:

Q1: What exactly is the inverse-Hessian estimand in the training-process comparison? Please specify the counterfactual process, the role of damping, and whether the reported quantity is a derivative or a finite behavior change. For the removal-versus-upweighting comparison, please also give the objective normalization and sign alignment explicitly.

Thank you for pointing out this ambiguity. The inverse-Hessian quantity is the parameter response to infinitesimal upweighting at the converged checkpoint, paired with the behavior gradient to obtain the local behavior derivative. It is not a finite behavior change. Without damping, the parameter response is

−HD−1∇θℓ(zk;θD).-H_{\mathcal D}^{-1}\nabla_\theta\ell(z_k;\theta_{\mathcal D}).

The training process comparison uses damping 0.010.01 for numerical stability, replacing HDH_{\mathcal D} with HD+0.01IH_{\mathcal D}+0.01I. Accordingly, exact computation here refers to the specified damped response. The factual solution is refined in double precision until its gradient norm falls below 10−1210^{-12}.

For objective normalization, we use

LD=1n∑iℓi+λ2∥W∥F2,Lup,k=LD+αℓk,L−k=1n−1∑i≠kℓi+λ2∥W∥F2.L_{\mathcal D}=\frac1n\sum_i\ell_i+\frac{\lambda}{2}\|W\|_F^2,\qquad L_{\mathrm{up},k}=L_{\mathcal D}+\alpha\ell_k,\qquad L_{-k}=\frac1{n-1}\sum_{i\ne k}\ell_i+\frac{\lambda}{2}\|W\|_F^2.

with unchanged regularization and unregularized biases. To align signs, we use negative cross-entropy for the loss behavior, and compute upweighting scores as Bup−BfactualB_{\mathrm{up}}-B_{\mathrm{factual}} and removal scores as Bfactual−BremovedB_{\mathrm{factual}}-B_{\mathrm{removed}}. Positive scores therefore indicate beneficial contributions to the selected behavior.

Q2: Can Proposition 1 be restricted to deterministic counterfactuals, or extended under appropriate assumptions for the expected estimand in Equation (1)? The remark about first-order approximations also needs qualification.

Thank you for identifying this scope issue. We have restricted Proposition 1 to deterministic counterfactuals and behavior evaluations, and clarified that nonlinear monotone transformations need not preserve rankings after taking expectations. We also agree that, for a fixed query at a common factual model, a transformation with positive derivative rescales all first-order scores by the same positive factor and preserves their ranking. We have corrected the accompanying remark accordingly.

Q3: How were TRAK and LESS adapted to each behavior surrogate? Please specify the training-side quantities, optimizer treatment, normalization, checkpoints, and aggregation over queries.

Thank you for requesting these implementation details. We adapt TRAK and LESS by replacing the query-side gradient with the gradient of each behavior surrogate, while keeping the training-side quantity fixed as the gradient of the mean full-response negative log-likelihood. LESS additionally uses the saved Adam second-moment estimates to precondition both training and query gradients. For consistent comparison across behavior surrogates, we do not apply additional unit-norm normalization to either side. Both methods use the final training checkpoint, and attribution scores are averaged equally over all the queries.

AuthorsOpenReview ↗

Response to Reviewer csRx (2/2)

Q4: For answer-token readouts, is the preceding rationale teacher-forced or generated? An answer-only negative log-likelihood baseline would help interpret the response-corruption results.

The preceding rationale is teacher-forced. Our answer-token readouts are conditioned on the query prompt and the provided reference rationale. In our experiments, "Answer logit" denotes the target answer token's score after log-softmax normalization over the answer candidates. We additionally compare it with answer-only negative log-likelihood (NLL) and raw logits, reporting AUPRC on Qwen3-8B over three seeds.

EstimatorAnswer-token readoutAnswer corruptionRationale corruption
GradSimCandidate-normalized Answer logit0.785 ± 0.0240.248 ± 0.001
GradSimNegative answer-only NLL0.779 ± 0.0240.248 ± 0.001
GradSimRaw logit0.401 ± 0.0100.269 ± 0.012
TracInCandidate-normalized Answer logit0.643 ± 0.0560.270 ± 0.010
TracInNegative answer-only NLL0.636 ± 0.0500.273 ± 0.010
TracInRaw logit0.281 ± 0.0350.370 ± 0.022
TRAKCandidate-normalized Answer logit0.941 ± 0.0060.169 ± 0.006
TRAKNegative answer-only NLL0.940 ± 0.0060.170 ± 0.006
TRAKRaw logit0.528 ± 0.0050.166 ± 0.015
LESSCandidate-normalized Answer logit0.877 ± 0.0200.198 ± 0.008
LESSNegative answer-only NLL0.875 ± 0.0210.199 ± 0.009
LESSRaw logit0.596 ± 0.0510.222 ± 0.022

Candidate-normalized answer logits and negative answer-only NLL yield nearly identical performance, while raw logits substantially reduce answer-corruption detection, further demonstrating the impact of behavior surrogate choice on attribution performance.

Q5: Could you sharpen the distinction from Bae et al. (2022)?

Thank you for highlighting this connection. Bae et al. (2022) distinguish practical influence-function estimates from LOO retraining and introduce the proximal Bregman response function (PBRF) as an alternative response that these estimates approximate. Our work extends this perspective across similarity-based, one-step, trajectory-based, and influence-function estimators through the specification S=(B,P,T)\mathcal S=(B,\mathcal P,\mathcal T) and a decomposition exposing the roles of behavior and training process. We further identify the often-overlooked role of behavior surrogates, showing that surrogate choice can reverse estimator comparisons and leave problematic training data largely undetected. We have revised the appendix to clarify this connection and these distinctions.

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

The authors significantly improved the writing in their rebuttal, and I have adjusted my score accordingly. Below are my reviews of the original submission.

The paper compares different "influence estimators" including the traditional influence functions, feature / gradient similarity, trajectory and LOO based influence estimates. A common framework is presented to tie the derivations of all of these influence estimates into a single family, and the different influences are compared empirically.

The papers main result is that each of these influence estimates is optimized to predict the effect of a different intervention on a different measured behavior of the model.

At a high level, I think the paper makes a good effort to address a fundamental question (even if the main result is not particularly unexpected), but this is severely undercut by poor writing which fails to properly explain / justify the actual experiments being performed or to convincingly connect the different influence estimates in a compelling manner.

Critical strengths

A Section 3-style derivation of all of the influence estimates as a single family would be very helpful in conveying the combination of different influence estimates into a single family that should be compared with one another, and clearly Section 5 is based on a significant amount of experimental work.

Critical weaknesses

However, I believe that the contributions of Section 3 are made much weaker by the poor writing. For instance, the derivation of influence functions goes to great effort to explain that the influence should scale with a gradient (equation 8), but then still appeals to other works for the equality R_T = H^{-1}. Other parts of the derivation were more self-contained and seem mathematically valid to me, but are not well written enough to provide clear insights beyond existing literature. I think that in order to be a valuable contribution, a rederivation of existing methods should be at least as (if not more) well written than previous derivations.

Similarly, from Section 5 it is clear that the authors ran a very impressive suite of experiments, but these experiments are not well motivated (e.g., what are the AUPRC / AUROC metrics? why are they the right metrics to support the claimed results? how should I interpret the tables and figures?). Section 4 has some of this contextualization (though there is room for improvement), but I did not see this being done in Section 5.

Finally, I found the claimed result to be somewhat unsurprising (different influence metrics are optimized to predict different effects so it is not surprising that each would be better at predicting its own effect). A good experimental validation of an unsurprising ("null") result is valuable, but I think that it raises the bar on the rest of the paper.

Questions for authors

See my notes on Section 5 above: Can you give better justification for the experiments you ran / context for interpreting their results?

4 comments
AuthorsOpenReview ↗

Response to Reviewer mcnf (1/2)

Thank you for your detailed feedback and for recognizing the importance of the question and the potential value of a unified analysis. We have revised Section 3 to clarify the derivations and insights, and Sections 4–5 to explain our motivation, findings, and their practical implications. Below are our responses to the issues raised:

W1: The derivation of influence functions goes to great effort to explain that the influence should scale with a gradient (equation 8), but then still appeals to other works for the equality RT=H−1R_T = H^{-1}.

Thank you for pointing out this ambiguity. This part of Section 3 extends the one-step decomposition to parameter responses induced by different training processes. We now explicitly expand the parameter response previously summarized by RT\mathcal R_{\mathcal T} into contributions propagated through subsequent training updates. The inverse-Hessian response underlying standard influence functions is only a special case corresponding to infinitesimal upweighting at a single converged stationary point. We also clarify how differentiating the stationarity condition yields this response.

The revised decomposition makes this distinction explicit:

dB(q;θk,T(α))dα∣α=0=∇θB(q;θD)⊤⏟behavior gradient⋅[−∑t=0T−1ηtAT←t+1∇θℓ(zk;θk,t(0))]⏟parameter response.\left.\frac{dB(q;\theta_{k,T}(\alpha))}{d\alpha}\right|_{\alpha=0}=\underbrace{\nabla_\theta B(q;\theta_{\mathcal D})^\top}_{\text{behavior gradient}}\cdot\underbrace{\left[-\sum_{t=0}^{T-1}\eta_t A_{T\leftarrow t+1}\nabla_\theta\ell(z_k;\theta_{k,t}(0))\right]}_{\text{parameter response}}.

Here, AT←t+1A_{T\leftarrow t+1} propagates perturbations through subsequent training updates. At a single stationary point with an invertible Hessian, the local stationary-point response is −HD−1∇θℓ(zk;θD)-H_{\mathcal D}^{-1}\nabla_\theta\ell(z_k;\theta_{\mathcal D}).

W2: The derivations are not written clearly enough to provide insights beyond existing literature.

We have revised Section 3 to make three insights explicit that, to the best of our knowledge, have not been jointly and systematically articulated in prior work:

  • Connecting similarity-based and learning-based estimators. Our decomposition places feature similarity and learning-based scores within a common structure, exposing the behavior and training signals omitted by similarity alone. This reveals a failure mode when examples with similar features have different label-dependent effects on the target behavior.
  • Interpreting comparisons across estimator families. A shared attribution target does not imply that the baselines measure the same influence. Our specification framework and decomposition make these differences explicit, showing which arise from behavior, intervention, or training process choices and which concern approximation of a fixed quantity.
  • Making the role of behavior surrogates explicit. The decomposition exposes how the behavior signal determines which model changes count as influence. This highlights an often-overlooked specification choice, particularly when a differentiable surrogate is needed, and explains why improving parameter-response estimation alone cannot resolve a mismatch between the surrogate and the attribution objective.
AuthorsOpenReview ↗

Response to Reviewer mcnf (2/2)

W3: The Section 5 experiments are not well motivated (e.g., what are the AUPRC / AUROC metrics? why are they the right metrics to support the claimed results? how should I interpret the tables and figures?).

Within each attribution task, different estimators are evaluated against the same objective (i.e., identifying problematic training data), while previous studies often adopt query loss as the default behavior surrogate. Our experiments examine how specification choices affect their performance under this shared objective. We have clarified the experimental motivations in Section 5:

  • Noisy label detection provides a standard classification setting with clearly defined ground-truth corruption labels. We use it to compare estimator families, with particular emphasis on how behavior surrogate choices affect their detection performance.
  • Response corruption extends the comparison to generation tasks with more diverse problematic data, testing how estimator and surrogate choices affect their detection.
  • Conditional backdoors test a more complex setting where harmful behavior depends on both the input context and the response, examining how specification choices affect attribution beyond response errors alone.

As all methods are evaluated against the same known corruption labels, AUPRC and AUROC measure detection quality across thresholds, while top-k precision measures detection under a fixed inspection budget.

We also clarify how to interpret the results. Table in Section 5.1 shows that changing the surrogate can reverse estimator comparisons (Finding 3), while the accompanying figure relates ranking differences to removal–retraining outcomes and robustness. The response-corruption figure shows that a single surrogate can detect some errors well while missing others (Finding 4). The backdoor table shows why poor performance under a default surrogate need not imply that an estimator is ineffective. In our setting, changing the surrogate raises TracIn’s AUPRC from 0.481 to 0.872, while benign-trigger controls expose false positives from representation similarity. These results challenge the generality of prior conclusions about estimator effectiveness (e.g., representation similarity performs well on backdoor detection while TracIn does not).

W4: The claimed result to be somewhat unsurprising (different influence metrics are optimized to predict different effects so it is not surprising that each would be better at predicting its own effect).

The observation that different estimators capture different effects emerges from our specification framework and decomposition, rather than constituting our main conclusion. In practice, these estimators are compared against the same attribution objective, yet their performance differences alone do not explain why they succeed or fail. Our contribution goes beyond making their estimation targets explicit. We identify structural limitations that more accurate estimation alone cannot resolve:

  • Label-agnostic similarity omits task-relevant signals. It cannot distinguish examples with identical features but opposing label-dependent effects. Computing similarity more accurately cannot resolve this limitation.
  • Improved estimation need not improve attribution. Reducing inverse-Hessian–vector product error improves approximation to a fixed response, but cannot resolve a mismatch between that response and the attribution task. Our framework makes the underlying estimation target explicit.
  • Behavior surrogate choice is an overlooked specification axis. To the best of our knowledge, we are the first to systematically characterize its role across influence estimator families. Even with an accurate parameter response, the chosen surrogate can obscure harmful data or reverse estimator comparisons under the same task objective.

These limitations have not, to our knowledge, been systematically characterized across estimator families through a common specification framework.

Reviewer_mcnfOpenReview ↗

The writing is much better, but the results are still underwhelming in my opinion

I thank the authors for taking the reviews into account and for the significant effort they put into improving the quality of the paper. The new version looks significantly better.

However, in my opinion the main weakness (namely that it does not seem surprising that different notions of influence would disagree) still stands.

Taking both of these into account, I plan to increase my score from a 1 to a 2 (weak reject).

Thank you for reviewing the revised manuscript and acknowledging the improvements. We sincerely appreciate your reconsideration. A concrete example may help clarify our contribution.

In noisy label detection, representation similarity, one-step gradient scores, and influence functions are used to identify the same mislabeled training examples. When their calculated influence rankings differ, task performance alone does not explain the reason. Our framework shows that label-agnostic similarity ignores learning signals and can therefore fail to distinguish examples with similar features but different labels. It also explains why one-step gradient and influence function estimators can produce different rankings because of their different parameter responses, even though both define influence through changes in the same test loss.

The decomposition also highlights behavior surrogate choice as an important but often-overlooked factor. Changing only the surrogate can reverse the relative performance of estimators on the same task, while a single surrogate can leave some types of problematic data largely undetected in complex scenarios.

Our contribution is therefore to explain differences among commonly used estimators and show how overlooked choices affect their practical evaluation. The key finding is not that different quantities disagree, but that comparisons on the same attribution task can lead to different conclusions about which estimator works better because of specification choices that are often left implicit.

Reviewer_RobuOpenReview ↗
Rating
3
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper presents a systematic study of specification mismatch in influence estimators and examines why different estimators may give different importance rankings of data. The paper first shows that different influence estimators (e.g., representation-based and gradient-based estimators) can be decomposed into behaviour (e.g., change in a query), intervention (e.g., the action taken on a training sample, such as removing or upweighting it), and training process (e.g., a gradient step). The paper then systematically toggles all three components, showing the effect of each component on ranking mismatch. In particular, the paper shows that i) the choice of specification significantly affects influence rankings, ii) under a fixed specification, approximation error grows with distance from the linearization point, which distorts rankings, and iii) behaviour surrogates are task-dependent.

Critical strengths

The strengths of the paper are as follows:

  1. The decomposition of different influence estimators is a useful tool for analyzing and understanding the estimators themselves, and it serves as a nice reference for data influence and attribution researchers.
  2. The study of the decomposition and its components is systematic and yields interesting insights.
Critical weaknesses

The weaknesses of the paper are as follows:

  1. The paper would benefit from another round of polishing. In particular, the notation could be reorganized and the exposition made clearer. Furthermore, for readers who may be less familiar with the data attribution literature, it would be beneficial to describe concepts such as leave-one-out loss and standard influence functions in the appendix.
  2. While the insights in this paper are nice, the paper would be more impactful if it offered more practical guidance for researchers choosing between data influence estimators. For instance, given the claim that “Behaviour surrogates should be chosen jointly with the estimator and target task,” it would be helpful to know which behaviour surrogates should be used for which target tasks, especially for downstream LLM applications such as pre-training vs. post-training data curation.
Questions for authors

None

2 comments
AuthorsOpenReview ↗

Response to Reviewer Robu (1/1)

Thank you for your thoughtful review and constructive suggestions. We appreciate your recognition of our framework as a useful tool for understanding influence estimators and as a reference for data influence and attribution researchers, and we are glad you found our systematic study insightful. Below are our responses to the issues raised:

W1: The paper would benefit from another round of polishing. In particular, the notation could be reorganized and the exposition made clearer.

Thank you for this helpful suggestion. We have consolidated the general notation at the beginning of Section 2, removed repeated definitions, and revised the exposition in Section 3. We also added a notation table at the end of the appendix for convenient reference.

W2: For readers who may be less familiar with the data attribution literature, it would be beneficial to describe concepts such as leave-one-out loss and standard influence functions in the appendix.

Thank you for this suggestion. We have expanded the appendix section “Background and Relation to Prior Work” to introduce LOO attribution and derive standard influence functions.

W3: While the insights in this paper are nice, the paper would be more impactful if it offered more practical guidance for researchers choosing between data influence estimators. For instance, it would be helpful to know which behaviour surrogates should be used for which target tasks, especially for downstream LLM applications such as pre-training vs. post-training data curation.

We agree that practical guidance would strengthen the paper. Our experiments offer empirical observations toward this goal. In classification tasks, logits are often worth exploring as an alternative to the default loss. In generation tasks, surrogate choice depends more strongly on the task, as a single surrogate can leave some types of problematic data largely undetected. Our results also motivate using trajectory information from multiple checkpoints when available, given the strong performance of trajectory-based attribution. These observations suggest evaluating estimator–surrogate combinations on a validation set covering the error types relevant to the task. Our LLM experiments cover post-training data curation through instruction tuning. We will explore extending this analysis to larger-scale pre-training data curation in the future.

Reviewer_RobuOpenReview ↗

Reviewer Response

Thank you for providing your clarifications. The notation revisions make the paper clearer -- thank you for taking time to make these adjustments.

I will keep my score, but I look forward to seeing this analysis extended to larger-scale pre-training data curation, and other applications in the future!

Comments on the paper

1 comment
AuthorsOpenReview ↗

General Response

We thank the reviewers for their thoughtful feedback and constructive suggestions. Robu recognized our framework as a useful tool for understanding influence estimators and as a reference for data influence and attribution researchers, and found our systematic study insightful. csRx recognized our controlled experiments separating specification mismatch from approximation error, found the interactions between estimators and behavior surrogates informative, and acknowledged the experimental support for our practical findings. mcnf recognized the importance of the question and the potential value of a unified analysis, while requesting clearer derivations and experimental interpretation.

Our revisions clarify the paper's motivation and contributions, make the insights from the unified decomposition explicit, and explain how the experiments support these insights and inform practical comparisons of influence estimators. The main revisions are:

  • Clearer derivations and insights in Section 3. We rewrote the trajectory decomposition, added an explanatory figure, clarified its relationship to influence functions and TracIn, and made the limitations of label-agnostic similarity explicit.
  • Clearer experimental motivation and interpretation in Sections 4–5. We distinguish controlled comparisons of specification mismatch and approximation error from practical evaluations against a shared attribution objective, highlighting estimator ranking reversals and the limitations of using a single behavior surrogate.
  • Technical clarifications. We clarify the mathematical definitions, implementation details, and evaluation procedures underlying our analysis and experiments.
  • Improved accessibility and positioning. We consolidated notation, expanded the background on LOO and influence functions, and clarified our distinctions from prior work.

We have uploaded a revised manuscript, with substantive revisions highlighted in blue.

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

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