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Under review as a conference paper at ICLR 2027

Do Learned Particle Dynamics Transfer Across Battery Operating Conditions?

Abstract

Machine-learned simulators of physical systems are usually trained and tested under similar conditions, yet for batteries what matters is how electrode particles behave when the charging rate, temperature or cell age changes, and such measurements are scarce. We introduce a benchmark of operando optical microscopy movies, recorded while the batteries run, in which the same particles are filmed under different conditions: 22 graphite particles at slow (C/20) and faster (C/2) charging over 6–45 °C (about 300 hours of recording), 24 particles of a nickel manganese cobalt oxide (NMC) cathode at three rates, and four further cells. Forecasters predict a particle's future image from its recent frames and the known current, and are compared with baselines that replay the same particle's earlier behaviour. First, with one training rate, a network that steps forward in charge passed rather than in time transfers far better from slow to fast charging (graphite: skill gains of 0.42 and 0.51 over matched time steps at short and long horizons), because charge builds in the known speed-up. Second, same-particle baselines largely catch up with a step-by-step network at long horizons, whereas a U-Net that predicts each horizon directly stays ahead on six graphite rate and temperature splits but does not clearly beat NMC's best baselines. Third, particles first convert during lithiation in a reproducible order at one rate and temperature but not detectably across rates, and forecasts from slow to fast charging miss when and where particles convert, relative to a repeat experiment. For the foundation model Poseidon, performance depends strongly on how the output is scaled; Poseidon beats the direct U-Net at short horizons when data are scarce, but under the tested recipes neither Poseidon nor Walrus beats it at long horizons.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
operando microscopy, battery materials, scientific machine learning, spatiotemporal dynamics prediction, generalization under distribution shift, physics-informed baselines, experimental data, electrochemistry

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.50 over 4 reviews, above 68% of the others.
Reviewer_iULcOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2(+1)
Soundness
3
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Paper summary

The paper presents a benchmark of real operando iSCAT microscopy movies that capture the same battery electrode particles under various operating conditions. It includes 22 graphite particles tested at different charging rates and temperatures. The objective is to predict a particle's future image after a specific amount of additional charge has passed, using its last four frames and the known current as inputs. Evaluation is conducted through transfer splits based on rate, temperature, particle type, and cycle. The key contributions of this work are a comprehensive dataset; a controlled comparison of models that predict future behavior based on charge increments versus time increments; strong non-neural baselines such as the replay of the same particle’s previous behavior and a mean-only predictor; and an assessment of the PDE foundation models Poseidon and Walrus. The findings reveal that predicting charge-transfer performance more effectively across slow-to-fast charging is limited to a single training rate. Additionally, a direct-prediction U-Net consistently outperforms the best baselines on graphite, although results are less conclusive for NMC. Furthermore, forecasts struggle to accurately predict both the timing and location of particle transformations, which may be influenced by variability in repeated experiments.

Critical strengths
  • The benchmark proposed in the paper is based on approximately 300 hours of operando iSCAT recordings, which capture the same particles under various charging rates, temperatures, and cycles. This allows for a clear distinction between changes in operating conditions and changes in the observed objects.
Critical weaknesses
  • The paper is very difficult to follow due to its reliance on 100+ pages of appendices and 120+ tables, with many key claims supported only by appendix results. Findings labeled as "descriptive," "retrospective," or "exploratory" are often reported briefly, leading to confusion about which conclusions are well-supported.
  • The proposed benchmark is framed as a test of whether learned particle dynamics transfer across operating conditions, but it doesn’t clearly explain why forecasting iSCAT images is the right way to measure this, or what a well-transferring forecaster would enable. The forecaster requires operando iSCAT frames as input, which means it can only be used in specialized laboratory settings and cannot be applied to deployed batteries. Its value therefore lies in research applications, such as replacing costly experiments at new conditions or guiding experimental design. Unfortunately, the paper doesn’t specify which of these it targets, nor does it justify the main task choices (4 history frames, forecast horizons, and raw optical contrast as the target) in relation to any of them.
Questions for authors
  1. Could the authors clearly indicate in the main text which claims are supported by resolved, prospective evidence and which are exploratory or retrospective? Could they also move the key supporting results from the appendix into the main text?
  2. The coupled step-and-history analysis in Appendix J found that fewer history frames gave higher skill than the default k=4k = 4 (e.g., +0.13+0.13 with k=2k = 2). Could the authors report an ablation that varies k at a fixed step size, preferably on the transfer splits, to justify k=4k = 4?
  3. About the forecast horizons: What scientific or practical consideration motivated the horizons of 0.01 to 0.32 of the reference half-cycle capacity?
  4. Since the optical contrast is not a calibrated lithium fraction, why is the main focus on predicting raw images instead of quantities that have more physical relevance, such as transition timing or switch maps? Would the rankings of the models change if transition timing were the primary metric?
8 comments
AuthorsOpenReview ↗

Reply to Reviewer iULc

Thank you for saying clearly which parts were hard to follow; we organised the revision around them.

W1 and Q1. Evidence status in the main text, and key results moved there. Sec. 7 now opens with Table 3 (p. 10), which gives each finding with its key numbers, evidence status (defined in Sec. 4 and the caption) and location. Finding 1, the role of a second training rate and the graphite part of Finding 2 are resolved and prospective: a forecast uses only information available when it starts, within an offline benchmark whose outlines, alignment and part of the calibration are built from completed acquisitions (Appendix B.3). Some splits train on, or replay from, acquisitions recorded after the test acquisition; Appendix B.4 rescores replay with earlier recordings only, and Appendix B.5 records the origin of each reference capacity. The NMC part of Finding 2 is not resolved. Conversion order is resolved within one electrode, and its check against the acquisition history is resolved with all runs but not without the two recovery runs (Sec. 7). The transition forecasts are retrospective; full rollouts of the step-by-step U-Net from C/20 to C/2 also fall short of repeat agreement in lithiation (timing error 0.105 against 0.030), whereas in delithiation the two errors are similar (0.026 against 0.022; Table 51). The foundation-model comparison is exploratory. The main text also gains the cell-history checks (Sec. 7) and the acquisition timeline (Fig. 1e).

W2. What a transferring forecaster would enable, and the task choices. We target the second use you name, guiding experimental design, and Sec. 1 now says so. One slow half-cycle takes about a day to record (the movies here cover 544 hours, 527 of them new; Table 4), so forecasts from the first images at an untested rate or temperature could help decide which conditions to image. Their usefulness for choosing experiments has not been evaluated, and Finding 3 shows that slow-to-fast forecasts still miss when and where particles convert. Sec. 4 now gives the evidence behind each task choice (Q2–Q4 below).

Q2. History length at a fixed step. With the charge step fixed at 0.005 of the reference capacity, we varied k over 1, 2, 4 and 8 on four graphite splits, including both rate-transfer directions, and one NMC split (three seeds, paired windows; Appendix I.5, Tables 60–61). At Δ = 0.02, four frames are best or equal-best on every graphite split: one frame loses 0.11–0.25, and two or eight lose at most 0.03. At Δ = 0.16 the effect depends on the split: from C/20 to C/2 other lengths beat four by 0.04–0.08 (resolved for one and two frames), four frames are best on new-particle fold 0 (five particles, descriptive), and the other differences are about 0.02 or smaller. On NMC, eight frames beat four by 0.02 [0.01, 0.04] at Δ = 0.02. The +0.13 for k = 2 in the former Appendix J came from the same-rate C/20 split, where the step size changed too; at a fixed step, two frames gain at most 0.04 [0.04, 0.05] (C/20 → C/2, Δ = 0.16). Four frames are therefore a reasonable choice at short horizons on graphite.

Q3. What motivated the horizons. The horizons are a doubling grid from 0.01 to 0.32 of the reference capacity, a benchmark convention whose endpoints were not derived from the physics; Sec. 4 now simply states what they span. The shortest covers a few stored frames at every rate, and the longest about a third of a slow half-cycle and the whole of the shortest half-cycles (C/2 at 6 °C). Measured afterwards on the same-condition repeats, the strongest optical change takes a median of 0.05 to 0.11 of the reference capacity to sweep across a particle (Appendix C), so the two shortest horizons fall within one conversion and the two longest exceed it.

Q4. Why images, and would the rankings change under transition timing? We forecast images because they keep the pattern within each particle, and pixel error, transition timing and switch maps all follow from one image forecast, whereas a timing model gives no spatial information. The rankings change in part, as Sec. 6.3 now says. For C/20 → C/2 lithiation forecast from a fixed start, where 80–88% of the targets lie beyond the direct U-Net's trained horizons, the direct U-Net and cross-rate replay have similar timing errors (0.037 and 0.038), the step-by-step U-Net is worst (0.073), and replay has better switch maps (ρ 0.14 against 0.01 for both U-Nets), so timing as the primary metric would keep the direct U-Net ahead of the step-by-step U-Net and similar to replay. In a retrospective check that starts each forecast just before its transition, within the trained range, the direct U-Net has the smallest timing error (0.039 against 0.051 for replay; difference −0.012 [−0.024, −0.000]) and a higher but unresolved map correlation (0.18 against 0.08). No forecaster reaches repeat agreement (0.025 and 0.33; Tables 54 and 55).

Thank you for the response and the revision. Adding Table 3, which provides the evidence status for each finding, along with the fixed-step history ablation and clarification of the target use, addresses several of my concerns. I have a few remaining points I would appreciate clarification on:

  1. Physical readouts vs. pixel skill: In the fixed-start comparison, which does not use the observed future, cross-rate replay matches the direct U-Net on transition timing (0.038 vs. 0.037) and produces better switch maps than both U-Nets. How do the authors reconcile this with Finding 2? Does it suggest that, for the stated purpose of guiding experiment selection, the learned models add little beyond simple replay?

  2. History length: The new ablation varies kk only for the step-by-step U-Net, and on the headline C/20→C/2 split, one or two frames outperform four at Δ = 0.16. Does the direct U-Net’s lead over the best baselines hold for other history lengths?

  3. Target use vs. task design: The stated use is forecasting from the first images at a new condition, but forecast origins start at u0u_0 = 0.14. Could the authors explain how the current task setup reflects that use, or whether forecasts from earlier origins were evaluated?

AuthorsOpenReview ↗

Reply to Reviewer iULc (follow-up)

Thank you very much for the follow-up. Here are the further clarifications you requested:

Readouts and Finding 2. Finding 2 is about pixel skill at leads up to 0.32 Qref, the range the direct U-Net was trained on. In the fixed-start comparison (origin at the frame at or before u = 0.14), 80–88% of the C/20 → C/2 transition targets lie beyond that range (Appendix H.2), and in this comparison replay is as good on timing and better on switch maps. In a retrospective check that starts each forecast just before its transition, within the trained range, the direct U-Net has the smaller timing error (0.039 vs 0.051; difference −0.012 [−0.024, −0.000]) and a higher but unresolved map correlation (0.18 vs 0.08; Tables 54 and 55). The two comparisons also differ in origins and targets, so they do not isolate the effect of lead length. On your second question: yes, for choosing experiments from the first images, the learned models we tested add little over replay from a fixed early start, and none reaches repeat agreement on these C/20 → C/2 lithiation targets. This is part of Finding 3, and it is why we recommend comparing learned forecasters with same-particle replay (Sec. 7).

History length. We trained the direct U-Net with 1, 2 and 8 frames (fixed step 0.005 Qref, seeds 0–2) on the four graphite splits of Table 60, and scored all history lengths and the baselines on the same windows. Lead over the strongest baseline at Δ = 0.16:

FramesC/20 → C/2C/2 → C/20New particles (fold 0)Later cycles
1+0.066 [0.016, 0.085]+0.173 [0.143, 0.250]+0.064 [0.048, 0.213]+0.155 [0.106, 0.223]
2+0.109 [0.033, 0.134]+0.173 [0.143, 0.250]+0.080 [0.065, 0.219]+0.166 [0.110, 0.239]
4+0.107 [0.034, 0.131]+0.174 [0.145, 0.257]+0.099 [0.085, 0.226]+0.165 [0.117, 0.231]
8+0.099 [0.035, 0.126]+0.174 [0.145, 0.254]+0.113 [0.089, 0.217]+0.162 [0.109, 0.232]

The lead holds for every history length (fold 0 has five particles and is descriptive). Unlike the step-by-step U-Net, the direct U-Net gains nothing from fewer frames: on C/20 → C/2, two and eight frames match four, and one frame is slightly lower (−0.040 [−0.048, −0.017]; one of its three seeds stopped early). At Δ = 0.02, four frames are best or equal-best on every split, and one frame falls below the best baseline on C/20 → C/2 (−0.078 [−0.098, −0.050]). With all five seeds on its own windows, the four-frame model reproduces the published C/20 → C/2 gain (+0.111 [0.046, 0.133]). The table, with the Δ = 0.02 results and the differences from four frames, is now Table 62 (Appendix I.5, p. 69) of the revised PDF. The code and job list are in the anonymous code repository (scripts/rebuttal/direct_history.py).

Earlier origins. Yes. Table 33 (p. 44) scores the trained models from requested origins starting at u₀ = 0.05. On C/20 → C/2, for origins between 0.05 and 0.14 the direct U-Net leads the best baseline by +0.21 [0.19, 0.25] at Δ = 0.02 and +0.17 [0.15, 0.20] at Δ = 0.16, more than at later origins, and the charge clock still leads the time clock. This uses a shifted origin lattice, so it is descriptive. The fixed-start transition forecasts above are the closest match to the use we describe and the lattice did not start earlier than u = 0.05.

Reviewer_HUMSOpenReview ↗
Rating
2
Confidence
1
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

Modern lithium-ion batteries commonly use graphite anodes and nickel manganese cobalt oxide (NMC) cathodes. During charging and discharging (lithiation and delithiation of the electrode material), particles undergo changes in their optical properties that can be observed using operando optical microscopy.

The authors introduce a benchmark of 2D microscopy videos, represented as tensors of shape T×1×H×WT \times 1 \times H \times W. For the primary graphite dataset, they record the same electrode particles under different operating conditions in a single battery cell, identify and segment individual particles, and extract their image sequences. They also reprocess an existing NMC microscopy dataset from [1] and incorporate measurements from four additional cells.

The authors evaluate various neural networks, statistical baselines, and pretrained physical foundation models for predicting future particle images (optical contrast) from four recent observations and additional information, such as the particle mask and operating conditions.

Their experiments establish three main findings.

First, a neural network trained at one charging rate (e.g., C/20) generalizes substantially better to another rate (e.g., C/2) when predictions advance by a fixed amount of accumulated charge rather than physical time.

Second, simple baselines that replay the previous behavior of the same particle become competitive with autoregressive neural networks at long forecasting horizons. Direct multi-horizon prediction with a U-Net performs better on graphite, mitigating autoregressive error accumulation, but does not consistently outperform strong baselines on NMC.

Third, graphite particles undergo phase transitions in a reproducible order under the same operating conditions, but this ordering is not detectably preserved across different charging rates. Neural networks struggle to predict when and where these transitions occur, even when their overall image-reconstruction accuracy is relatively high.

References

[1] Xu, Chao, et al. "Operando visualization of kinetically induced lithium heterogeneities in single-particle layered Ni-rich cathodes." Joule 6.11 (2022): 2535-2546.

Critical strengths

1. Novel experimental dataset and benchmark. The authors introduce a valuable benchmark based on operando optical microscopy, including previously unpublished graphite measurements and reprocessed NMC data. A particularly important feature is that the same particles are observed across different operating conditions, enabling the evaluation of learned dynamics under distribution shifts while controlling for particle identity. Collecting such experimental data is expensive and technically challenging, making the dataset a potentially useful resource for the scientific machine-learning community.

2. Extensive empirical evaluation and informative findings. The paper provides a comprehensive comparison of neural forecasting architectures, statistical baselines, and pretrained PDE foundation models across different charging rates, temperatures, and forecasting horizons. The evaluation includes strong same-particle replay baselines, several robustness checks, and comparisons against experimental repeatability. Importantly, the experiments reveal limitations of existing approaches, particularly their difficulty in predicting the timing and spatial patterns of physical phase transitions. These findings provide useful guidance for developing and evaluating future models.

Critical weaknesses

1. Insufficient justification of the benchmark's broader scientific and practical relevance. Although the authors introduce an interesting real-world forecasting task, they do not sufficiently explain why accurately predicting changes in particle optical contrast is scientifically or practically important. In particular, it remains unclear how successful image forecasting could contribute to understanding battery degradation, improving charging protocols, or identifying physical mechanisms. The experiments provide useful insights into the performance of different forecasting methods, but the paper could better establish why this particular task is important for the broader scientific machine-learning community. This limits my confidence in the potential impact and future adoption of the benchmark.

2. Presentation and organization of the paper and supplementary material. The paper would benefit from a clearer presentation of its main contributions and experimental findings. The abstract mixes newly collected graphite measurements with previously published NMC data without clearly distinguishing their origins. It also enumerates several rather different findings, including charge-based forecasting, comparisons of neural architectures, particle phase transitions, and foundation-model adaptation, without sufficiently emphasizing the central contribution or the overall message.

Some methodological details are also difficult to locate. For example, the skill metric is introduced in Section 4 without clearly identifying it as an established forecasting metric or citing [1], despite including this reference in the bibliography. Some sentences are unnecessarily long (e.g., lines 64–67), and Section 3 would benefit from a figure explaining the experimental setup, particle identification, and construction of the forecasting dataset.

The appendix is unusually extensive (approximately 105 pages beyond the main paper) and contains numerous exhaustive experimental tables, implementation details, and overlapping sensitivity analyses. While I appreciate the authors' emphasis on reproducibility and transparency, this makes it difficult to locate and verify the evidence supporting the main conclusions. I encourage the authors to consolidate the appendix around the essential experimental protocols, statistical analyses, ablations, and robustness checks. Detailed implementation configurations, sweep commands, and exhaustive per-model/per-horizon results could instead be provided through the accompanying code repository and machine-readable supplementary files. Importantly, the analyses concerning information leakage, experimental confounding, statistical independence, and baseline fairness should remain directly accessible in the appendix.

References

[1] Murphy, Allan H. "Skill scores based on the mean square error and their relationships to the correlation coefficient." Monthly weather review 116.12 (1988): 2417-2424.

Questions for authors

1. Experimental protocol and acquisition order. How did the authors decide the order in which different charging rates (C/20, C/2, and 2C) and temperatures were applied to the same cell? Since the acquisitions were performed sequentially, could the ordering influence the observed differences in particle dynamics and the conclusions about cross-condition generalization?

2. Battery degradation and its influence on the results. Did the authors measure or estimate battery degradation over the repeated charging and discharging cycles, for example through changes in capacity or voltage profiles? If so, how significant was the degradation, and to what extent could it explain the differences observed across charging rates? Can these effects reasonably be neglected in the reported experiments?

3. Scientific and practical utility of the benchmark. What concrete scientific or practical applications could benefit from accurately forecasting the optical evolution of electrode particles? In particular, how closely does performance on the proposed image-forecasting task reflect a model's ability to predict physically meaningful quantities, such as phase-transition dynamics or battery degradation?

4 comments
AuthorsOpenReview ↗

Reply to Reviewer HUMS

Thank you for the careful reading, including the appendix.

W1 and Q3. Why forecasting optical contrast matters. The abstract and Sec. 1 now explain this. The intended use is planning experiments in operando imaging: one slow half-cycle takes about a day to record (the movies used here cover 544 hours, 308 of them on the main graphite electrode; Table 4, p. 17), so a forecaster that predicts each particle's response from the first images at a new rate or temperature could help decide which conditions to image. We have not tested whether forecasts improve that choice; the benchmark measures how accurate they are.

The images also give two readouts that pixel error does not show: the charge at which each particle's staging transition occurs, and a switch map of the charge at which each pixel changes fastest. They do not track pixel skill closely. From C/20 to C/2, cross-rate replay trails the direct U-Net in pixel skill (0.61 against 0.79 at Δ = 0.16), yet on the lithiation transition targets, forecast from a fixed start and mostly beyond the direct U-Net's trained horizons, it has a similar timing error (0.038 against 0.037) and better switch maps (ρ 0.14 against 0.01). No forecaster reaches the agreement between repeated experiments (0.026 and ρ 0.34; Sec. 6.3, Table 54), so the benchmark reports pixel skill, timing and switch maps together.

W2. Presentation.

  • The abstract now separates the new graphite movies from the published NMC movies (Xu et al., 2022) and states one central result.
  • Sec. 4 defines skill as the mean-squared-error skill score of forecast verification and cites Murphy (1988).
  • The sentence at lines 64–67 is now two sentences.
  • Fig. 1 has a new row (p. 4): panel e shows the 18 acquisitions in recording order with their conditions and retained particle movies, and panel f shows how a forecast window is built. Panel a shows the atlas that identifies particles across acquisitions. The figure does not show the optical setup, which is similar to that of Han et al. (2026) (Sec. 3).
  • As you suggested, the appendix is now a core of 54 pages, down from about 105, with a guide at its start (p. 15) from the main-text claims to their evidence. The appendix keeps the analyses you named: leakage (Appendix B), confounding (Appendices A and G.8; Sec. 7), statistical independence (Table 29) and baseline fairness (Appendix C). The full result grids are in the supplementary Extended results.

Q1. How the acquisition order was chosen, and whether it matters. The 18 acquisitions were recorded one after another and make up the cell's whole cycling history (Fig. 1e). Rates went from slow to fast so that a slow cycle on the nearly fresh cell was used for optical calibration and each block followed a slower one, which leaves less lithium behind after delithiation; the carry-over was assumed small and was not measured. The C/20 and C/2 blocks end with a 25 °C cycle, and the temperature order was not chosen to test a hypothesis (Appendix A). Because condition and history are confounded in this cell (Secs. 4, 7), we compared conversion order between acquisitions equally far apart in the sequence: same-rate pairs agree (Kendall τ 0.42 [0.16, 0.62]) and cross-rate pairs do not (0.02 [−0.15, 0.20]; difference 0.40 [0.05, 0.69]). Without the two recovery runs described under Q2, the difference keeps its sign but is not resolved (0.26 [−0.15, 0.53]), so other history effects remain possible (Appendix G.8). When replay may use only movies recorded before each test acquisition, no gain of the direct U-Net over the strongest baseline decreases (Appendix B.4, Table 13).

Q2. Degradation, and whether it can be neglected. No impedance was measured, so the charge passed and the voltage profiles are our record of how the cell changed (Appendix A). The first and last C/20 acquisitions at 25 °C pass 276.8 and 276.2 µAh on delithiation, with voltage profiles within 5 mV (root mean square), and lithiation passes 5.6% less in the later one. Four consecutive C/2 cycles at 25 °C pass 174–178 µAh, and the third and fourth cycles of the four-cycle 2C acquisitions differ by at most 1.5%, whereas rate and temperature change the passed charge two- to threefold. These comparisons show modest drift at matched conditions, but they cannot show that degradation is negligible or separate it from condition and history over the whole sequence. One event cannot be neglected: the C/2 cycle at 6 °C probably plated lithium, and the next two 25 °C acquisitions were recovery runs that started partly lithiated (Sec. 3, Appendix A). They are the only C/20 → C/2 test acquisitions in which the step-by-step U-Net falls below the particle-mean ridge with a resolved interval at Δ = 0.16 (Table 27). Without independent degradation labels, the benchmark cannot test degradation prediction.

Thank you for the detailed rebuttal and the improvements to the manuscript. I appreciate the effort involved in reorganizing the appendix, clarifying the experimental protocol, and addressing the other reviewers' and my own questions.

Nevertheless, I still find the main paper rather difficult to follow. In particular, the presentation often emphasizes detailed numerical comparisons and experimental qualifications instead of developing a clear narrative around the central contribution and its scientific significance.

I would encourage the authors to consider benchmark papers such as RealPDEBench (ICLR 2026) [1] and The Well (NeurIPS 2024) [2] as examples of clearer presentation. These works first motivate the need for the benchmark, then introduce its structure and evaluation protocol, and finally summarize the principal empirical findings.

In the current manuscript, a dedicated figure illustrating the complete forecasting pipeline and a more focused discussion of the main experimental conclusions could substantially improve readability, particularly for readers outside the battery-science community.

Overall, while I acknowledge the value of the collected dataset and the extensive experimental evaluation, I believe the manuscript still requires a major revision of its writing and overall organization to communicate its contributions effectively. In my view, these are not merely minor presentation issues, as the current structure makes it difficult to assess the broader significance of the work. Therefore, despite the improvements and the authors' thoughtful responses, I have decided to maintain my original score and continue to lean toward rejection rather than acceptance.

References

[1] Peiyan Hu, , Haodong Feng, Hongyuan Liu, Tongtong Yan, Wenhao Deng, Tianrun Gao, Rong Zheng, Haoren Zheng, Chenglei Yu, Chuanrui Wang, Kaiwen Li, Zhi-Ming Ma, Dezhi Zhou, Xingcai Lu, Dixia Fan, Tailin Wu. "RealPDEBench: A Benchmark for Complex Physical Systems with Real-World Data." The Fourteenth International Conference on Learning Representations. 2026.

[2] Ohana, Ruben, et al. "The well: a large-scale collection of diverse physics simulations for machine learning." Advances in Neural Information Processing Systems 37 (2024): 44989-45037.

AuthorsOpenReview ↗

Reply to Reviewer HUMS (follow-up)

Thank you for the follow-up and for acknowledging the value of the dataset and the experimental evaluation. We have uploaded a revision that takes up your suggestions. Following RealPDEBench and The Well, Sec. 1 (pp. 1–2) now explains why the benchmark is needed, what it contains and how forecasts are scored, and then the main findings. A new figure, Fig. 2 (p. 4), shows the whole pipeline, from a split on the same particles to the forecast window, the forecasters and the scores. The experiments and conclusions are unchanged.

Like RealPDEBench, and unlike the simulations collected in The Well, the benchmark is built on measurements. Its distinctive feature, which your first review singled out, is that learned dynamics can be evaluated under distribution shift while controlling for particle identity, and repeated graphite experiments give a reference for the errors. That design is what makes the results relevant beyond batteries.

With one training rate, the step-by-step U-Net transfers from C/20 to C/2 far better when it steps in charge passed than when it steps in time, because at constant current counting charge builds in the known speed-up. At long horizons, replaying the same particle's history largely catches up with the step-by-step U-Net, while a U-Net that predicts each horizon directly stays ahead on five of six graphite rate and temperature splits, which suggests that benchmarks of measured dynamics need same-object baselines. Forecasts from C/20 to C/2 with good pixel skill still miss when and where particles in the main graphite cell first convert during lithiation, compared with a repeat experiment, so pixel error alone cannot show whether a model has captured the dynamics.

Those two readouts matter for batteries because how fast a cell can charge and how long it lasts depend on how its particles take up lithium.

Dear Reviewer HUMS,

Thank you again for the concrete suggestions in your follow-up. We acted on them in the revision: Sec. 1 (pp. 1–2) is now organised like the two benchmark papers you recommended, and the new Fig. 2 (p. 4) shows the whole forecasting pipeline. If you have time before the discussion closes, we would value your view on whether the paper is now easier to follow.

Kind regards,

Authors

Reviewer_4jqmOpenReview ↗
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3
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2
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2
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3
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Paper summary

This paper introduces a benchmark for studying whether learned forecasters of battery electrode-particle dynamics transfer across operating conditions. Using operando interferometric-scattering (iSCAT) microscopy, the authors re-observe the same particles under multiple charging rates, temperatures, and cycles: 22 graphite particles across C/20, C/2, and 2C (about 300 hours of recording) and 24 NMC particles at three rates, plus four additional cells. The forecasting task predicts a particle's future image from its recent frames and the known current. The authors compare charge-based and time-based stepping (clocks), autoregressive and direct multi-horizon U-Nets, several strong same-particle baselines (including replay of the particle's own history), and two pretrained PDE foundation models (Poseidon and Walrus). Three findings emerge: (1) with a single training rate, stepping in charge transfers far better than stepping in time; (2) strong same-particle baselines largely catch up with the autoregressive network at long horizons, while the direct U-Net stays ahead on graphite but not clearly on NMC; and (3) the order and location of particle phase conversion are reproducible within one condition but not across rates, and slow-to-fast forecasts miss them relative to a repeat experiment. The contribution is the data and the evaluation methodology, not a new architecture.

Critical strengths
  1. The dataset is genuinely scarce and valuable: it re-observes the same particles across conditions, which cleanly separates "condition 2, change" from "object change" in a way most distribution-shift benchmarks cannot.
  2. The evaluation methodology is exemplary: paired particle-level confidence intervals, strong same-particle baselines, a repeat experiment as a reference for reproducibility, and explicit leakage controls.
  3. The findings are non-obvious and actionable, especially the charge-clock result and the demonstration that simple baselines nearly match autoregressive networks at long horizons.
  4. The paper is honest about limitations and provides an anonymized, reproducible protocol with code and data.
Critical weaknesses
  1. The main graphite results rest on a single field of view and a single cell with sequential recordings, so operating condition and cell history are confounded; this limits causal claims about transfer.
  2. The NMC dataset is third-party, and on NMC the learned models do not clearly beat simple baselines, so the positive claims rest heavily on one material.
  3. The charge clock is a repurposing of well-established battery practice (charge-based time axes) rather than a new insight, and it only applies to constant-current segments.
  4. The foundation-model evaluation may understate pretraining benefits because results depend strongly on adapter design and output scaling.
Questions for authors
  1. The abstract opens by stating that learned simulators are usually trained and tested under similar conditions, but it does not state the concrete value of the benchmark. Could the authors add one sentence naming the downstream battery-engineering capability this benchmark is meant to enable (e.g., faster-charging protocol design, lifetime/aging prediction, safer operation)?
  2. Finding 1 shows that a time-clock model trained at several rates and given the rate/step sizes — the (d, s, r) condition on NMC, C/3+1C→2C — largely closes the gap to the charge clock. Could the authors quantify, as a function of the rate gap, the minimum training-data recipe (how many distinct rates, which rates, and how much data per rate) needed for a time-clock model to match the charge-clock model? This would turn the qualitative "multi-rate training can partly replace the charge clock" into a concrete statement about what data to collect for transfer.
  3. The model's condition inputs are (d, s), optionally extended to (d, s, r) (log rate, log step time, log step charge). Could the authors report the marginal contribution of each of these three added signals separately (rate only, step time only, step charge only) on cross-rate skill, rather than only the aggregate (d, s, r) gain? This would identify which inductive signal actually drives transfer, and whether "log step charge" and "log rate" are redundant once the charge axis is used.
  4. Is the charge-clock advantage purely a time-rescaling effect? A direct control would be a time-clock model whose step size is rescaled by the known rate so its step duration matches one charge step (a rate-adaptive time step). If this does not recover the full charge-clock skill, the charge axis contributes something beyond a faster clock. Could the authors report this ablation?
  5. The paper's stated contribution is the benchmark, not a new method. Given that, would the authors consider establishing a single consistent upper reference for future work by running the current strongest baselines — the direct U-Net with (d, s, r) conditioning, history-aligned replay, and a foundation model with a matched/stronger adapter — uniformly across all transfer splits and both materials, and additionally reporting the two non-pixel metrics (switch-map correlation and transition-timing error) for these baselines? This would make the conclusions independent of which baseline happens to be strongest on any given split, and would give future methods one clear target to beat on every axis.
4 comments
AuthorsOpenReview ↗

Reply to Reviewer 4jqm (part 1 of 2)

Thank you for the specific questions. Each one led to new analyses, described below; Q2 and Q5 can be answered only in part.

W1. Condition and cell history are confounded. We agree, and Sec. 7 says so. Two checks argue against a simple drift through the sequence as the cause of the lost agreement across rates, although neither can separate rate from cell history. At the start and end of the C/20 block, delithiation passes nearly the same charge (276.8 and 276.2 µAh) and lithiation 5.6% less (Appendix A). Conversion order also agrees more between acquisitions at the same rate than between pairs at different rates that are equally far apart in the sequence (difference in Kendall τ 0.40 [0.05, 0.69]; Appendix G.8). Without the two 25 °C runs that followed the probable lithium plating at 6 °C, the difference keeps its sign but is not resolved (0.26 [−0.15, 0.53]), so other history effects remain possible. All models are scored on the same recorded test windows, so model comparisons are paired within the cell. The charge clock also leads when the test block lies between the training blocks in recording order (+0.40 [0.26, 0.53]) and when it comes before them (+2.57 [2.27, 3.11]). Appendix F.2 (Table 46) now lists the electrodes on which each finding was tested.

W2. NMC is third-party, and learned models do not clearly beat simple baselines there. The abstract and Sec. 1 now state that the NMC movies were published before (Xu et al., 2022). They make up 17 of the 544 hours of recording; the other 527 hours, from five cells, are new (Table 4, p. 17). The charge-clock result holds on both materials (NMC +0.52 [0.46, 0.55] at Δ = 0.16). The direct U-Net's long-horizon lead over same-particle baselines is presented as a graphite result, in the abstract and in Table 3, which also shows the unresolved NMC gains (+0.01 and +0.03 at Δ = 0.16). NMC changes smoothly, so simple extrapolation is a strong baseline there (Secs. 6.2, 6.5).

W3 and Q4. Charge axes are standard; is the advantage only a rescaling of time? We agree that charge axes are standard in electrochemistry, and Sec. 4 now says so. At constant current the answer is yes, by construction: a time step rescaled by the known current, Δt = ΔQ/I, picks the same frames as the charge clock, so the rate-adaptive control you propose is the charge-clock model (Sec. 4). Finding 1 measures what this rescaling is worth to learned simulators: +0.42 [0.38, 0.44] at Δ = 0.02 and +0.51 [0.37, 0.56] at Δ = 0.16 over a time clock matched to the training rate (Sec. 6.1). The two can differ only when the current changes within a run, so we forecast the constant-voltage holds of the 2C runs (three particles; retrospective, because the charge horizons use the measured future current). There, U-Nets trained only at constant current score 0.49 to 0.77 with the charge clock, against 0.24 to 0.61 for the best baseline, but neither this gap nor the lead of the charge clock over the time clock is resolved (Table 41).

Q1. A sentence on the downstream capability. The abstract now reads: 'a forecaster that transfers could use the first images at a new condition to help decide which day-long experiments to pursue, for example when studying faster charging' (also Sec. 1). The benchmark has no independently verified plating, safety or end-of-life labels, so we do not claim protocol design or lifetime prediction. Its later-cycle split tests transfer to later cycles of the same cell, which is different from predicting ageing.

AuthorsOpenReview ↗

Reply to Reviewer 4jqm (part 2 of 2)

Q2. The training recipe a time clock needs. Only in part. We measured the effect of training coverage at the recorded rates, but these rates cannot identify a minimum recipe (Sec. 6.1; Appendix E, Tables 37, 39 and 42).

  • For single-rate transfer on both main electrodes, the time clock trails the charge clock at a new rate even when both are given the rate and step sizes ((d, s, r); Table 37).
  • With two training rates that both cover the particle population, a time clock with (d, s, r) shows no resolved difference from a charge clock with the same inputs on NMC (+0.01 [−0.02, 0.04] at Δ = 0.16). Compared with the default charge clock, its deficit grows from 0.04 [0.03, 0.06] when all 42 1C particles are used to 0.16, 0.22 and 0.26 [0.19, 0.41] with 12, 6 and 3. Graphite shows the same trend, descriptively, on its three 2C test particles.
  • On the temperature and later-cycle splits the test rate equals a training rate. There the time clock with (d, s, r) matches or is slightly ahead of the charge clock at C/2 and on later cycles but trails it by 0.35 at C/20, and a second training rate does not consistently help it: on later cycles its skill falls from 0.88 to 0.48.

With three rates per material we cannot say how the requirement scales with the gap between rates or which rates are best; Appendix E states this.

Q3. Each added signal alone. We ran each signal alone with the time clock (Appendix E, Table 38). With one training rate (graphite C/20 → C/2), none closes the gap: the charge clock stays at least 0.41 ahead of every variant at Δ = 0.16. With two (NMC C/3 and 1C → 2C), step charge alone leaves no resolved difference (+0.01 [−0.03, 0.03]), rate alone leaves 0.06 [0.04, 0.08], and step time, which is constant under a time clock, adds nothing resolved. Under the charge clock the step charge is constant and rate and step time carry the same information, so we did not test them separately there; added together, they lower its skill at Δ = 0.16 from 0.67 to 0.55 on graphite (Table 30).

W4 and Q5. Adapter dependence, and one consistent reference. In part. The pixel-skill references now cover every Table 2 split. The two non-pixel metrics are reported wherever transition records exist: for the step-by-step U-Nets, history-aligned replay and three further baselines on graphite and NMC splits (Tables S39–S51), and for the direct U-Net between C/20 and C/2 only (Table 54). The comparison with same-condition repeats is still limited to graphite targets and does not include the foundation models.

The pixel-skill reference is the direct U-Net with (d,s) and five seeds. At Δ = 0.16 it leads the best baseline on five of the six graphite rate and temperature splits (+0.11 to +0.21; Tables S6–S7 and S10) and on new particles (+0.09 [0.08, 0.14]). On the same-condition repeats it leads at C/20 (+0.14 [0.02, 0.17]; Table S8) and trails at C/2 (−0.04 [−0.08, −0.01]; Table 2), where one of its five seeds kept its initial checkpoint. With (d,s,r) it is worse on all nine splits tested at Δ = 0.16 (Table 40). ConvLSTM also covers every Table 2 split.

We agree that the foundation-model results depend on the adapter, and Secs. 6.4 and 7 restrict the conclusion to the adaptations we tested. Output scaling raises Poseidon-T by 0.10–0.18 at Δ = 0.16 on three of the four reference splits (Tables 20–21), and with one C/20 acquisition the original Poseidon-T leads the direct U-Net at Δ = 0.02 (+0.19 [0.16, 0.27]). As you suggested, output-scaled Poseidon-T now covers every Table 2 split. At Δ = 0.16 it leads the direct U-Net on NMC 2C → C/3 (+0.08 [0.04, 0.19]) and on the C/2 repeat (+0.10 [0.09, 0.12], where one U-Net seed kept its initial checkpoint), and has lower point estimates on the other five (three resolved, later cycles unresolved, new particles descriptive; Table 26). Poseidon-B and -L trail the direct U-Net by 0.01–0.05 on the four reference splits (Table 25). The adapters receive no particle outline (Sec. 5), so better adaptations may change this.

The transition readouts are compared with repeat agreement on graphite targets that have a same-condition repeat; the foundation models were not scored on them. From a fixed start (C/20 → C/2 lithiation), the timing errors are 0.037 for the direct U-Net, 0.038 for cross-rate replay, 0.073 for the step-by-step U-Net and 0.026 between repeats. Most of these targets (80–88%) lie beyond the direct U-Net's trained horizons, and over all of them replay has the best switch maps (ρ 0.14 against 0.01; Table 54).

Dear Reviewer 4jqm,

We appreciate your helpful comments and have addressed your questions above. As the discussion phase is about to close, we would be grateful for any further feedback you may wish to share.

Kind regards, Authors

Dear Reviewer 4jqm,

Thank you again for your review. We hope our reply and the revision answer your questions. The new analyses include each conditioning signal on its own (Table 38), forecasts of the constant-voltage holds where the charge and time clocks can differ (Table 41), and output-scaled Poseidon-T on every split of Table 2 (Table 26). We would welcome your feedback before the discussion closes.

Kind regards,

Authors

Reviewer_UMwKOpenReview ↗
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Paper summary

The paper introduces a benchmark of operando optical microscopy movies of re-observed battery electrode particles, principally 22 graphite particles in one cell across charging rates and temperatures and 24 NMC particles across three rates, with smaller additional-cell evaluations. It compares autoregressive and direct neural forecasters, PDE foundation-model adapters, and strong statistical and same-particle replay baselines. The main findings are that charge-based stepping improves single-rate-to-new-rate forecasting under constant current; direct U-Net prediction retains a long-horizon pixel-skill advantage over baselines on several graphite splits, whereas NMC gains are less clear; and forecasts of graphite conversion timing and spatial patterns fall short of repeat-experiment agreement in the main slow-to-fast setting. The paper releases evaluation code and processed data for review and explicitly limits its claims to retrospectively curated movies.

Critical strengths

S1: Rare, well-controlled observational resource. Re-observing the same particles across operating conditions makes a useful distribution-shift benchmark possible. The authors provide careful acquisition and identity documentation, same-particle replay and particle-mean baselines, paired evaluation, and an input-exposure audit (Secs. 3–5; Appendices A–B). This is the strongest argument for acceptance.

S2: Supported empirical findings beyond the clock comparison. The direct U-Net improves on the strongest baseline by +0.11 skill for C/20 to C/2 at charge horizon 0.16; the acquisition-and-particle crossed 95% interval is [0.04, 0.14] (Table 44). The decomposition attributes 0.085 of the corresponding total gain of 0.111 to within-particle spatial residuals (Table 108), providing evidence beyond prediction of a particle's mean intensity. The repeat-experiment comparisons and foundation-model output-scaling analysis are also informative. The authors report unresolved NMC gains and weak conversion-map transfer candidly (Secs. 6.2–6.5).

Critical weaknesses

W1: Independent replication is limited for the findings that carry the main scientific interest. The main graphite comparisons are carefully controlled, and Table 44 supports their numerical robustness within the measured electrode. However, the 22 particles come from one field of one cell, with rate conditions acquired in successive blocks (Sec. 3; Table 3). As the authors explicitly acknowledge in Sec. 7, rate and cell history are confounded; resampling particles and acquisitions cannot resolve that confounding or establish reproducibility across cells. The additional graphite cells are useful checks, but each contributes only one flake. On cell B, favorable charge-versus-time clock ordering depends on retrospective capacity matching, and transferred models fall below persistence on both first formation cycles (Sec. 6.5; Appendix A.1). The authors appropriately restrict their transition-order and map conclusions to the main electrode. My concern is that, even within this stated scope, the limited independent replication constrains how much general scientific insight can be drawn from the benchmark and reduces the significance of the demonstrated transfer results.

W2: The additional empirical lessons have useful but limited demonstrated breadth. The paper explicitly contributes data and evaluation rather than a new architecture (Sec. 1), and I assess it on that basis. Under constant current, charge stepping incorporates a known rate-dependent rescaling, which the authors correctly distinguish from learning rate dependence (Sec. 4). The acceptance case therefore rests substantially on the resource and findings beyond that rescaling: direct prediction's graphite gains, repeat-referenced conversion errors, and sensitivity of foundation-model adaptation. These are substantive contributions, but the strongest resolved advantages are concentrated in the main graphite electrode; at horizon 0.16 the direct model does not clearly beat the strongest NMC baselines, and the second NMC electrode favors AR(2) over direct prediction (Secs. 6.5 and 7). NMC gains do appear at horizon 0.32, so the limitation is their consistency across settings. The task also supplies retrospectively constructed geometry, alignment and some calibration (Table 12), which further bounds its practical interpretation. Taken together, the demonstrated breadth of the empirical lessons falls below my acceptance threshold, despite the value of the measurements and controls.

Questions for authors
  1. Which clock-ordering and model-versus-baseline conclusions are supported using a reference capacity fixed without the evaluated acquisition's endpoint, and which require retrospective matching? Please distinguish comparisons that preserve the same physical forecast origins and targets from comparisons where changing the capacity also changes the physical prediction horizon.

  2. Table 12 states that chronological precedence of reference movies is not checked. For the existing acquisitions, how would the strongest replay baseline and the direct model's relative gains change if reference movies had to precede the test acquisition? This is particularly relevant to C/2-to-C/20. If this constraint leaves no eligible reference movie for a split, please state that explicitly.

4 comments
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Reply to Reviewer UMwK (part 1 of 2)

Thank you for the careful review, and for assessing the paper as a contribution of data and evaluation. Both questions led to new analyses (Q1 in Appendix B.5, Tables 14 and 15; Q2 in Appendix B.4, Table 13). When replay may use only earlier recordings, no gain of the direct U-Net decreases, and the clock conclusion and the direct U-Net's gain from C/20 to C/2 rest on reference capacities that do not come from the evaluated acquisitions. Neither analysis replaces the independent replication discussed under W1.

W1. Independent replication is limited. We agree, and Sec. 7 says so. Appendix F.2 now lists, for each finding, the electrodes on which it was tested and what each test showed, including the tests that do not support it (Table 46).

The charge clock's lead after training at one rate is resolved on the main graphite electrode and on the published NMC movies, a second material and cell (24 particles; +0.52 [0.46, 0.55] at Δ = 0.16). The direct U-Net's lead is resolved on the main graphite electrode and, by a small margin, on the later cycles of the NMC811 cell (60 particles; +0.04 [0.03, 0.06]). The findings on conversion order and transition timing are not replicated: they need several particles with staged transitions and repeated acquisitions at each rate in one field of view, which only the main graphite electrode provides. Your statements about the further graphite cells are correct: cell B shows the favourable clock ordering only with the matched capacity, so we do not count it as support (Q1), and the transferred networks fall below persistence on both first formation cycles.

As you say, resampling cannot separate rate from cell history. The clock and model-versus-baseline comparisons are paired on identical forecast windows, so both sides see the same particles at the same point in the cell's history. The charge clock also leads when the test block lies between the training blocks in recording order (+0.40 [0.26, 0.53]) and when it comes before them (+2.57 [2.27, 3.11]). None of these checks shows that the sizes of the effects would recur in another cell.

A replication would need a second field of view in which several particles are followed through repeated acquisitions at two or more rates, with the rates interleaved. The main series alone took 308 hours of recording. Two further graphite cells were recorded for 175 hours, but each field yielded only one quantifiable flake, below our pre-registered minimum of eight objects (Table 4; Appendix A.1), so they cannot test the conversion-order and timing findings.

W2. Breadth of the empirical lessons. We agree with your account of where the direct model's advantages hold, and the abstract, Table 3 and Table 46 state it. The lead is resolved on eight of the eleven main-electrode graphite splits at Δ = 0.16, although one of these, to 2C, rests on three particles and is descriptive. On the published NMC movies it is resolved in both directions at Δ = 0.32 but in neither at Δ = 0.16, and AR(2) leads on the second NMC electrode.

Beyond the rescaling, the published NMC movies show how much training coverage a time-stepped model needs and how strong simple baselines can be. At constant current the charge clock rescales time, but a time clock given the rate and step sizes still trails it on NMC by 0.04 [0.03, 0.06] when the second training rate is sampled on 42 particles and by 0.26 [0.19, 0.41] when it is sampled on three (Table 39). From C/3 to 1C and 2C, the direct U-Net reaches a skill of 0.91 at Δ = 0.16 (persistence scores 0) against 0.88 for the best baseline, so its margin of +0.03 [−0.002, 0.06] is small and not resolved (Table 2). Scoring learned models against baselines this strong is one of the lessons in Sec. 7.

We agree that outlines, alignment and part of the calibration are built from completed acquisitions (Table 12), and that this limits practical use. The same preprocessing and scoring outlines are used for every model and baseline (the foundation-model adapters do not receive the outline as an input; Sec. 5). After the analyses for Q1 and Q2, the graphite reference capacity was still chosen after the recordings were made, and in splits that run against the order of recording the networks are still trained on later acquisitions.

Finally, you describe the resource as the strongest argument for acceptance (S1), and its value does not depend on which forecaster does best on it. The movies cover 544 hours of recording, 527 of them previously unpublished (Table 4). The processed data, splits, baselines and evaluation code are available to reviewers, and the data will be released under CC BY 4.0, so any forecaster or further cell can be scored in the same way.

AuthorsOpenReview ↗

Reply to Reviewer UMwK (part 2 of 2)

Q1. Conclusions and the origin of the reference capacity. Appendix B.5 now gives, for each conclusion, where its reference capacity comes from (Tables 14 and 15). On each trained electrode one constant scales every acquisition (none is rescaled by its own capacity), and all methods of a split are scored on the same windows, so every comparison within a split keeps the same physical forecast origins and targets.

Graphite uses 280 µAh, a round value chosen after the recordings were made. It is typical of the slow half-cycles, is not the measured capacity of any acquisition, and reflects no evaluated acquisition in the splits that test no C/20 acquisition (C/20 → C/2 among them). The formation-cycle delithiation, which precedes every acquisition of these splits, passed 282.5 µAh (0.9% from 280 µAh), but the unit was not set from it. NMC uses the charge of the C/3 acquisition, which was recorded first, and the NMC811 cell uses a cycle recorded before every training and test cycle. With these constants the charge clock leads the time clock after training at one rate (+0.45 [0.35, 0.49] for graphite C/20 → C/2 and +0.52 [0.46, 0.55] for NMC at Δ = 0.16), and the direct U-Net leads the strongest baseline on graphite (+0.11 [0.05, 0.13]) but not on NMC (+0.03 [−0.00, 0.06]).

In the graphite splits that test C/20 acquisitions (C/2 → C/20 among them), the 280 µAh is typical of the tested acquisitions without being fitted to any one of them, and in the two reverse NMC splits the constant was measured on the tested acquisition. The clock conclusion rests on the forward splits and does not need these.

Only cells B and C are scored with two capacities. With a capacity from an earlier acquisition, the second formation cycle of cell C supports the clock ordering for networks transferred across rate (+0.96 to +1.72; all three seeds resolved) and the direct U-Net's lead (three of four seed intervals exclude zero). Cell B at C/2 supports neither; its favourable ordering requires the matched capacity, measured on the evaluated acquisition. Changing the capacity changes the physical horizon only in these two-capacity rows (20.2 against 26.0 µAh on cell B). On 501 origins of cell B with the same physical history and targets under both capacities, the ordering still requires the matched capacity (−0.15 to +0.01 against +0.22 to +0.45 over three seeds), so the changed horizon does not explain it. This check covers the clock comparison only. No electrode was retrained with another constant, so sensitivity to its value is tested only on cells B and C.

Q2. Reference movies that precede the test acquisition. We rescored the fourteen splits of Table 13, allowing replay to use only movies recorded strictly before each test acquisition (Appendix B.4). Networks and fitted baselines are unchanged, and a replay baseline with no eligible reference returns persistence. No gain of the direct U-Net over the strongest baseline of any kind decreases: at Δ = 0.16 it is unchanged on ten splits and larger on four, because the restriction removes or weakens the strongest replay baseline there. Four further comparisons are outside the table. In the later-cycle split and the two NMC811 splits on later cycles and higher cut-off voltages, every reference precedes the test movies by design, and the NMC811 new-particle fold was not rescored.

Four splits have no earlier reference movie: C/2 → C/20, C/2 at 25 °C → colder, NMC 2C → C/3, and 3C → 0.5C on the second NMC electrode. In C/2 → C/20, which you asked about, the strongest replay baseline (history-aligned replay, skill 0.46) is then unavailable, the strongest remaining baseline is the particle-mean ridge (0.34), and the direct U-Net's gain rises from +0.16 [0.13, 0.24] to +0.29 [0.25, 0.35]. In these four splits the networks and fitted baselines are themselves trained on later acquisitions, so the splits test the direction of transfer and do not represent a forecast that could have been made at the time.

In six splits all references are earlier (C/20 → C/2 among them), and nothing changes. In four splits some are, and the strongest replay baseline weakens on three and gains 0.01 on the fourth. Across temperature at C/20, for example, it falls from 0.38 to 0.32 and the gain rises from +0.11 [0.06, 0.19] to +0.17 [0.09, 0.23].

As a check made after the results were known, we also scored existing networks trained only on earlier acquisitions on two temperature splits. The direct U-Net's gain stays resolved at Δ = 0.16 (+0.089 [0.003, 0.155] at C/20 and +0.124 [0.081, 0.175] at C/2) but is not resolved at Δ = 0.02. The new-particle folds train and test on the same acquisitions and cannot be placed in recording order without retraining.

Dear Reviewer UMwK,

We appreciate your helpful comments and have addressed your questions above. As the discussion phase is about to close, we would be grateful for any further feedback you may wish to share.

Kind regards, Authors

Dear Reviewer UMwK,

As the discussion closes in some time, we would like to check whether our reply answers your two questions. In short, the direct U-Net’s gains stay the same or grow when replay may only use recordings made before each test acquisition (Table 13, Appendix B.4). Appendix B.5 (Tables 14 and 15) shows where the reference capacity behind each conclusion comes from. We can still respond to any remaining point before the deadline. Thank you!

Kind regards,

Authors

Comments on the paper

2 comments
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Summary of the revision

We thank the four reviewers. All four see value in the same-particle data. The revision makes the purpose and presentation clearer and adds analyses of training coverage, adapter dependence, cell history, replay references recorded before the test data, the reference capacity and replication. The transition-order and map conclusions still rest on one field of view in one cell (Sec. 7, Table 46), and we have not tested whether forecasts improve the choice of experiments. Main-text sentences that changed, including small rewordings for clarity, are marked in blue; the appendix was reorganised throughout and is not marked. Numbers in brackets, here and in our replies to each reviewer, are 95% bootstrap intervals: over particles, paired when two forecasters are compared, or over acquisitions for the Kendall τ values of Appendix G.8. 'Resolved' means that the interval excludes zero.

  • Contribution and data (Sec. 1; Table 4, p. 17). The paper is an application and benchmark study, submitted under the primary area 'applications to physical sciences (physics, chemistry, biology, etc.)'. It contributes data, an evaluation protocol and empirical findings, including cases in which learned models do not beat simple baselines, and proposes no new architecture. The movies cover 544 hours of operando recording from 42 acquisitions on six cells; 527 of these hours, from five cells, have not been published before. On the main graphite electrode, 22 particles (three of them also at 2C) are followed through 258 particle movies at rates from C/20 to 2C and temperatures from 6 to 45 °C (308 hours), so one condition can be held out at a time and repeated experiments give a reference for forecast errors. The processed data are available to reviewers through the anonymous links in the reproducibility statement and will be released under CC BY 4.0 with the final version; the splits, baselines and evaluation code are in the supplement.
  • Purpose and message (abstract, Sec. 1). As Reviewers 4jqm, HUMS and iULc asked, the abstract and introduction now state the intended use (deciding from the first images at a new rate or temperature which day-long experiments to run). They also separate the new graphite movies from the published NMC movies, and the abstract gives one central result.
  • Presentation. In response to Reviewers HUMS and iULc, Fig. 1e–f (p. 4) shows the acquisition sequence and how a forecast window is built, Sec. 4 (p. 5) gives the evidence behind the task choices, and Table 3 (p. 10) lists each finding with its key number and evidence status. The core appendix is now 54 pages, down from about 105, and the guide at its start (p. 15) links the main findings to their evidence. The full result grids are in a separate 74-page Extended results document (supplement/extended_results.pdf in the supplementary ZIP), and all results are also given as CSV files.
  • New experiments. The new analyses use about 450 further training runs; their job lists are in the supplementary code (configs/sweeps/RB_*). Each reply reports the analyses its reviewer asked for. We also forecast through the constant-voltage holds and, as Reviewer 4jqm suggested, ran output-scaled Poseidon-T on every Table 2 split, where it leads the direct U-Net on two of the seven (Table 26).
  • Replay references, reference capacity and replication (Appendices B.4, B.5 and F.2). In answer to Reviewer UMwK, we rescored fourteen splits that compare the direct U-Net with the baselines, allowing replay to use only movies recorded before each test acquisition (Table 13). No gain over the strongest baseline decreases, and the four splits that have no earlier reference are named. Tables 14 and 15 give, for each conclusion, where its reference capacity comes from, and Table 46 lists for each finding the electrodes on which it was tested and the outcome, including the tests that do not support it. These analyses reuse the trained networks.
  • Correction. On the interpolation split (C/20 and 2C to C/2), the learned models had been trained without the 2C recordings that the baselines used. After retraining with them, the charge clock still leads the time clock (+0.40 [0.26, 0.53] at Δ = 0.16), step-by-step models given the rate and step sizes become unstable across seeds, and the direct U-Net's lead over the best baseline falls from 0.10 in the submitted version to 0.06 [−0.04, 0.12]. It now leads on five of the six graphite rate and temperature splits (Appendix E).
AuthorsOpenReview ↗

Latest revision and further questions

We have uploaded one more revision. It adds Table 62 (Appendix I.5, p. 69), which shows that the direct U-Net's lead over the strongest baseline holds for 1, 2, 4 and 8 history frames, in answer to Reviewer iULc's follow-up. Apart from a short paragraph on p. 67 that points to it, the rest of the PDF is unchanged.

Reviewers 4jqm, HUMS and UMwK: if anything in our replies is unclear, or a point remains open, please let us know. We will be glad to clarify it before the 18th November deadline. Thank you!

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

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