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Paper summary
The paper argues that research on time series attribution asks the wrong question. Most work asks which method (Shapley, Owen, Banzhaf) is correct and how to compute it fast. The authors show that the result depends on setup choices: what replaces a masked value, which model output is tracked, and how coalitions are sampled. They then propose a different question: how much of the model’s behaviour can an explanation of a given size capture? They measure this as error against the number of values the explanation contains. On several UEA and MIMIC-III models, they find that low-rank explanations do better than additive or local ones, and that perturbation metrics such as keep loss cannot tell good attributions from random ones. Finally, they propose a fast learned explainer that also reports how well it fits each input.
Critical strengths
A clear new way to compare explanations:
Plotting error against explanation size puts all explanation types on one scale. The result holds on new inputs and new coalitions. A rank-1 explanation beats a local (lag-1) one on four of five models while using 1.7–9× fewer values.
It shows that rankings change with the setup, not only values:
Changing the masking baseline from zero to first observation gives a Kendall τ of only 0.267. Earlier time series work shows that the perturbation choice changes evaluation scores. This paper goes further and shows that it also changes the attributions themselves.
Honest work:
The paper reports hypotheses that failed (Kronecker structure, stable rankings, the Owen estimator), uses oracle-vs-random controls for the metric study, and reports that audit-guided repair does not beat random selection.
Critical weaknesses
Only two model types, and the TCN appears on one dataset only:
All seven UEA black boxes are GRUs. The only TCN is on MIMIC-III, and the main rate–distortion study uses only GRUs. The paper does not explain this choice. Transformers and CNN-based classifiers such as InceptionTime or ResNet are standard in time series classification and likely create different interaction patterns. The one TCN result already looks different: its rank-1 energy share is 0.245, compared with 0.53–0.77 for the GRUs. The claims “locality is the wrong structure” and “low rank is the right one” may therefore describe GRUs, not time series models in general.
The main result may also depend on the setup:
All error measurements use one setup: zero baseline, logit output and p = 1/2. But §7 shows that changing the setup moves the additive share by up to 32 points. The paper does not show that “low rank beats local beats additive” holds under other setups. Also, “rate” counts values, not how easy an explanation is to use. A rank-1 factorization is not clearly easier to read than a saliency map. The authors admit this, but there is no user study. Finally, the learned explainer fails on 2 of 6 models, and the paper has no way to predict where it will fail.
Key time series evaluation work is missing, so the novelty of §7 and §8 is unclear:
The paper says it makes the baseline problem and the weakness of perturbation metrics “operational for time series” (§2). But several papers already study perturbation-based evaluation of time series attributions: Turbé et al. (2023) evaluate post-hoc methods for time series classification against known ground truth; Schlegel & Keim (2023) study how the choice of perturbation affects time series XAI evaluation; Šimić et al. (2025) analyze many perturbation methods for validating attributions of neural time series classifiers; and Baer et al. (2025) show that perturbation effects differ by class. None of these is cited or discussed. The paper should explain what §7 and §8 add beyond this work. The §8 study is also small (one synthetic benchmark, five seeds), and the main keep-loss result is p = 0.058. Testing on the ground-truth benchmarks from these papers would make the metric claims much stronger.
Turbé, H., Bjelogrlic, M., Lovis, C., & Mengaldo, G. (2023). Evaluation of post-hoc interpretability methods in time-series classification. Nature Machine Intelligence, 5(3), 250–260.
Schlegel, U., & Keim, D. A. (2023). A deep dive into perturbations as evaluation technique for time series XAI. In World Conference on Explainable Artificial Intelligence (pp. 165–180). Springer.
Šimić, I., Veas, E., & Sabol, V. (2025). A comprehensive analysis of perturbation methods in explainable AI feature attribution validation for neural time series classifiers. Scientific Reports, 15(1), 26607.
Baer, G., Grau, I., Zhang, C., & Van Gorp, P. (2025). Class-dependent perturbation effects in evaluating time series attributions. In World Conference on Explainable Artificial Intelligence (pp. 292–314). Springer.
Questions for authors
Why are all UEA black boxes GRUs, and why is the TCN used only on MIMIC-III? Was this a compute limit or a deliberate choice?
Do the results in Tables 1 and 2 hold for a TCN or transformer black box on a UEA dataset?
Does the ordering “low rank > local > additive” stay the same under p = 0.25/0.75 or the first-observation baseline?
How do the findings in §7 and §8 differ from the perturbation-evaluation studies above (Turbé et al., 2023; Schlegel & Keim, 2023; Šimić et al., 2025; Baer et al., 2025)? Is the class-dependent effect reported by Baer et al. also visible in your gauge results?
Why does the learned explainer fail on Libras and JapaneseVowels, even though a per-input rank-4 fit reaches distortion 0.18 on JapaneseVowels (§9)?
The rate–distortion study is limited to P ≤ 300 (§11). What does a full pairwise fit cost in time and memory at that size, and can the method scale further?
4 comments
W3 / Q4: perturbation-evaluation literature, Baer et al., and the size of §8. Thank you for the references. All four are now cited, and Related Work keeps two questions apart. Turbé et al., Schlegel & Keim and Šimić et al. use perturbation scores to evaluate attribution methods. Our §7 is about something else: the masking convention changes the attributions themselves, both their values and their rankings. §8 then gives a case with exact ground truth in which a perturbation score does not track whether an attribution is correct.
On Baer et al., we looked in two places. First, per-input τ between the two baselines does vary by class (class means −0.11 to 0.35 on Libras, 0.18 to 0.44 on ERing). With 32 inputs spread over up to 19 classes, however, a Kruskal–Wallis test reaches p < 0.05 only on ERing and RacketSports. We read this as consistent with Baer et al., but underpowered.
Second, the class sorting itself had a larger effect. On CharacterTrajectories the correlation between the certificate and convention sensitivity was 0.39–0.58 on class-0 inputs, and it is about zero on the stratified sample. On stratified inputs, an input's own additive share predicts its convention sensitivity on five of six models (ρ = 0.38–0.66). The certificate does so only on MIMIC-III and RacketSports. We have removed that claim, and §9 now presents the certificate only as a fidelity measure.
§8 now uses 20 seeds instead of 5. Paired over seeds:
- At additive weight 0, keep loss does not separate the oracle from a random attribution (mean difference +0.04, p = 0.77). The p = 0.058 we reported before does not hold up. We fixed no equivalence margin, so we do not take this as evidence of no effect. At weight 0.3 keep loss does separate them (p = 5e-8).
- Insertion and deletion AUC, AUPD and AUPP separate oracle from random at both weights (p ≤ 3e-4).
- The ground truth separates the Owen and flat estimators at both weights (Spearman +0.066, p = 2e-5, and −0.046, p = 4e-7).
- Only one perturbation score also separates them at each weight: deletion AUC at weight 0 (p = 0.025) and drop loss at weight 0.3 (p = 1e-5). Drop loss ranks them in the opposite order to the ground truth.
The revised §8 makes this narrower claim. We could not run the ground-truth benchmarks of Turbé et al. during the discussion period, and we agree they would make §8 stronger.
Q6: cost of the full pairwise fit, and scaling. For the held-out comparison (8 inputs, 10 decoders, one 12 GB Titan Xp plus CPU):
- ERing (P = 260): a run takes 50 min to 2 h 04 min, with 26.6 GB peak host memory.
- JapaneseVowels (P = 300): a run takes 1 h 08 min to 2 h 11 min, with 46.5 GB.
These figures are now in App. B.2. Memory is dominated by the Gram matrix of the degree-2 basis, which has about P²/2 columns (45,151 at P = 300). It therefore grows as P⁴, which is why the full-basis measurements stop at P ≤ 300.
The full basis is only needed to fit and certify every decoder in the comparison. A rank-r explanation itself has P·r numbers, and the amortized estimator never builds the basis; it runs at P = 768 on MIMIC-III. Fitting rank-r structure directly from coalitions would remove the limit. We have not done that yet, and the paper states the P ≤ 300 limit and the measured costs.
If something is still not convincing, please tell us, and we will work on it before the discussion closes.
Thank you for the detailed response and the new experiments, which address most of my concerns. I appreciate that the authors narrowed the claims to GRU models instead of presenting the GRU result as general, and that they reported the class-sorting issue openly. The Limitations should still state that the evaluation uses only five UEA datasets and MIMIC-III, includes no CNN-based classifiers, and tests non-recurrent models under a single setup. I keep my score.
Thank you for reading the revision and for the follow-up. We added the three points to the Limitations and uploaded the revised PDF. It now says that every model is a classifier on one of seven UEA archives or MIMIC-III, that the TCN is our only convolutional classifier (no InceptionTime or ResNet), and that each TCN and transformer is a single trained model measured under one convention. To be precise about the data, the GRUs cover seven UEA archives and the TCN and transformer comparison uses five of them. Nothing else changed in this revision.
Thank you for the careful review. You asked whether the structural results describe GRUs or time series models in general, and that was the right thing to ask. They describe GRUs. We tested this directly and narrowed the paper.
One change affects several numbers below, so we mention it first. Five of the UEA test splits are stored sorted by class, so our "first N inputs" covered only one to three classes. The general comment explains this, and every per-input number here has been re-measured on a fixed class-stratified sample. Both findings you singled out still hold. On the four non-PenDigits GRUs, rank-1 beats the lag-1 band while using 1.7–9× fewer numbers: it gains 10–21 points over additive, and the band gains 3–7 (Table 1). Kendall τ between the zero and first-observation baselines is 0.25 over eight models.
W1 / Q1–Q2: does the structure result hold for a TCN or a transformer? It does not. We had used the TCN only as a comparator on the clinical task, so the submission never tested this. We trained a TCN and a transformer on the same five archives (P ≤ 300, test accuracy 0.80–0.99) and repeated the held-out comparison on the same inputs (Table 2; per model in Table A.6):
*The largest rank whose rate does not exceed the band's.
The low rank-1 share on the TCN that you pointed to (0.245) was already a hint. TCN and transformer games are close to additive (additive distortion 0.03–0.17), and on them rank-1 loses to the band even though the band uses 1.6–9× more numbers. We checked whether a short receptive field could explain this. The TCN's 61 steps cover every sequence except ERing's 65, so it cannot. §5 is now titled "Which structure? It depends on the architecture". The abstract, contributions, related work and conclusion now claim the result for recurrent models only. We did not add InceptionTime or ResNet.
W2 / Q3: does the ordering survive other conventions? First, a correction to a number you quoted. On the stratified inputs the coalition measure moves the additive share by at most 14.0 points; we had reported 32. The bootstrap interval for this swing excludes zero on six of eight models (Table 3).
For the GRUs we reran the comparison under p = 0.25, under p = 0.75 and with the first-observation baseline (20 model × convention cells). The band beats additive on all 160 inputs. Low rank at matched rate beats the band on 157/160. Rank-1 alone beats it on 123/128 inputs of the four non-PenDigits GRUs (Table A.7). PenDigits (12/32) has only 8 steps, so a lag-1 band there is already almost global. TCNs and transformers were run under a single convention, and the Limitations say so.
On usability, we agree that rate counts numbers and says nothing about how easy an explanation is to read. We ran no user study, and the Limitations now state this too.
Q5: why does the estimator fail on Libras and JapaneseVowels when a per-input fit works? Your comparison points to the answer. The estimator can represent these games, but it does not generalize across inputs. On JapaneseVowels a per-input rank-4 fit reaches median distortion 0.11. The estimator's median R² is 0.85 on training inputs and 0.16 on test inputs (Libras: 0.73 and 0.07). The drop has two parts.
The first part is an offset of the whole coalition function on test inputs: 0.46–0.58 SD, against 0.01 on training inputs. This offset is the game's constant. No attribution contains it, so it lowers the fidelity score and leaves the attributions alone. Refitting only the intercept on 32 black-box queries per input brings median R² to 0.37 on Libras and 0.49 on JapaneseVowels. One extra scale takes JapaneseVowels to 0.61. The best any intercept and scale can do is 0.45 and 0.64, so 32 queries get most of the way there. The scale is positive on 93–100% of inputs, so on those inputs no attribution changes sign or rank.
The second part is that predicted and true values become less correlated (0.92 to 0.80 on JapaneseVowels, 0.86 to 0.67 on Libras). Recalibration does not help with this part, because it sits in the coefficients themselves.
The same analysis shows how to tell in advance whether the estimator will work. We trained it on 80% of the training inputs and scored the remaining 20%. Median R² was −0.32 to −0.01 on JapaneseVowels and 0.04–0.18 on Libras, against 0.55–0.57 on CharacterTrajectories and 0.72–0.89 on MIMIC-III. One RacketSports seed is a miss: 0.02 on held-out training inputs, but 0.24 on test. All of this is in §9 and App. J.7 (Table A.21).
The rest of our reply (W3/Q4 and Q6) is in the next comment.