acceptodds
Under review as a conference paper at ICLR 2027

BatteryOCV: A Paired Dataset and Benchmark for High-to-Low Rate Profile Reconstruction

Abstract

Battery measurements involve a trade-off between speed and diagnostic value. Higher currents shorten measurement time, but resistance, reaction kinetics, and ion-transport limits shift the measured voltage away from the low-rate reference used to study degradation. Lower currents reduce these effects and provide a more consistent diagnostic reference, but a complete low-rate charge-discharge measurement can take more than 40 hours. We ask how well this reference can be reconstructed from faster, lower-fidelity measurements of the same cell. BatteryOCV contains 182,519 high-rate cycle records and 1,894 repeated low-rate references from 404 industrial NCM/graphite cells, paired on the same physical cells as they degrade. The benchmark task predicts a measured low-rate voltage profile and its charge and discharge capacities from neighboring high-rate voltage cycles, using cell-disjoint splits. We compare signal-processing and classical controls with autoencoder and generative baselines. On unseen cells of the training design, copying, averaging, or smoothing the high-rate curves leaves the discrepancy from the reference largely unchanged, whereas learned mappings reduce it substantially, and a linear ridge model is competitive with the neural networks. Capacity and charge-aligned errors capture what profile error misses, and differential-voltage peak counts provide a coarse check of local features. On held-out product designs, errors increase markedly for both linear and neural models. BatteryOCV provides paired data and a fixed protocol for measuring how much of a slow diagnostic reference can be recovered from fast measurements.

Primary area:
datasets and benchmarks
Keywords:
multi-fidelity learning, time-series reconstruction, datasets and benchmarks, battery degradation, distribution shift, scientific machine learning

Reviews

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1234this paper, Bottom 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
Reviewer_QqPWOpenReview ↗
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3
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Paper summary

The paper introduces a dataset of 182,519 high-rate cycles and 1,894 periodic (0.05C) reference measurements for 404 industrial NCM/graphite cells spanning five anonymized product designs. The dataset benchmark consists of predicting a measured low-rate charge/discharge voltage profile, and two corresponding capacities, from a surrounding cluster of high-rate voltage profiles. The primary split is cell-disjoint in the dominant Model E (265/39/76 train/valid/test cells), with additional zero-shot transfer testing Model-E-trained methods on 24 cells from designs A--D. Constant, signal processing, nearest neighbor, ridge, autoencoder, VAE, GAN, diffusion baselines are tested on the profile, capacity, charge-aligned and DVA peak count errors. Much more effective than simply replicating or averaging high-rate profiles for unseen cells in Model E, learned input dependent mappings are still challenged by competitive ridge regression results. Substantially higher errors occur on held-out designs, with additional few-cell experiments in the supp. highlighting how a substantial part of the profile difference is a design level shift, even captured with support set mean.

Critical strengths
  1. The dataset allows a form of supervision not generally available in existing cycling datasets. That is, the high-rate/low-rate pairs on identical physical cells at equivalent life stages can be used to avoid mixing the rate effect with cell identity and degradation. The size, repeated use, and fixed-cell disjoint splits argue for a potentially useful benchmark contribution.

  2. Disciplined and revealing evaluation - with good simple baselines, e.g., ridge and input-independent means; multiple outputs and metrics; clear demonstration that neural/generative complexity is not necessarily helpful. Also, show profile vs. capacity ordering disagreement and very limited within-design success transfer to related product designs. This makes the benchmark more believable/useful.

Critical weaknesses
  1. The ML novelty is small, and the application usecase is not fully validated. This paper takes the standard supervised regression approach to curve reconstruction for high-to-low rate, where the authors examine the state of the art in linear/NN/AE/RNN/Transformer/VAE/GAN/diffusion models. So basically all of the novelty comes from the dataset and use-case framing.

  2. Mostly what I see in the experiments is performance on normalized curve level reconstruction error, not that the reconstructed profiles have kept the diagnostic information to be of use for their use-case of battery health monitoring. - The only local feature measure is peak count error (which doesn't account for peak position or amplitude), which is degenerately (a constant predictor has zero error on A--D) not accounting for e.g. peak position and amplitude. So this reduces the novelty in the approach, as well as the practical relevance.

  3. The generalizability to something more than a single product design is naturally constrained. - Model E provides 380/404 cells and 1,792/1,894 references. - For the hold-out designs, there are only 4--8 cells per design, and together they shift product design/capacity class/protocol mixture/degradation coverage (nothing has the more degraded tail of Model E). - So while it's a good signal to see how much the transfer gap is, one cannot attribute this and generalize that BatteryOCV is broadly representative of industrial NCM/graphite cells. And the fact that they don't expose physical voltage limits and details of design further restrict physical interpretation or cross dataset comparisons.

Questions for authors
  1. Could authors provide a local feature based metric that will penalize missing/extra peaks, as well as peak position and/or amplitude error (preferably with expert review or a subset downstream degradation mode analysis)? This will indicate for me how much I consider this as more of a diagnostic reconstruction benchmark versus normalized curve reconstruction benchmark.

  2. How much does the comparison of methods depend on correlation among multiple references of same test cell? Please provide paired uncertainty intervals where cells (not reference rows) are the resampling units. Perhaps a macro avg per cell so that cells with more RPTs aren't weighted higher?

  3. What specifically is being made available at publication (measurement file, split metadata, preprocessing/training/evaluation code, license, long term url). Will sufficient voltage window / protocol information be available so that users can convert normalized errors to physically meaningful units? Availability of dataset and useful documentation are quite important for contribution.

1 comment
AuthorsOpenReview ↗

Response to Reviewer QqPW

1. Local features and aging changes. We added a peak-matching metric that measures position error and penalizes missing or extra peaks (maximum matching distance and penalty both 0.05 in normalized capacity units). Amplitude and spacing are measured on matched peaks.

On E (76 cells), the matched-feature results are:

Feature MAETraining meanFixed Conv
Amplitude (370 references each)0.0300630.014955
Spacing (365/370 eligible references)0.0139470.013589

On A–D (24 cells/102 references), the training mean has zero peak-count error but penalized peak error 0.021411. Across nine distance/penalty settings, fixed Conv beats the E mean; Ridge has lower peak error than fixed Conv on E and A–D.

We also evaluated consecutive-reference profile changes and fitted a charge and discharge capacity slope for each cell:

Qc,b(n)≈ac,b+βc,bn,b∈{ch,dis}.Q_{c,b}(n)\approx a_{c,b}+\beta_{c,b}n,\qquad b\in\{ch,dis\}.

Slope error is reported in normalized capacity per 100 cycles:

Test setZero-slope controlFixed ConvDifference [95% CI]
E0.0171580.008330−0.008828 [−0.012456, −0.005105]
A–D0.0135310.017465+0.003934 [0.001033, 0.006722]

On E, fixed Conv reduces successive-profile-change RMSE from 0.005106 to 0.003299 across 294 pairs. On A–D, it is worse than zero change (0.004734 versus 0.003780; 78 pairs). The model captures some aging-related changes within E but not reliably across designs. Electrode degradation modes were not independently expert-labeled.

2. Cell-level uncertainty. For target-based metrics, we average seed scores, then references within each cell, then cells equally. Paired intervals resample whole cells with all repeated references (5,000 resamples). The E peak-error difference between fixed Conv and the training mean is −0.008042 (95% CI [−0.009476, −0.006555]). Intervals cover variation among evaluated cells; seed variation is treated separately.

3. Data and release. BatteryOCV provides repeated high-rate/0.05C measurements for 404 industrial NCM/graphite cells across five product designs. Model E contributes 380 cells and A–D just 24, limiting conclusions about product transfer.

The anonymous review link provides the normalized HDF5 and split metadata. The supplementary ZIP accompanying this response adds 69 completed ablation runs, predictions, evaluation code and table-generation scripts, and includes an MIT code license. Dataset licensing and a permanent URL are pending. Physical voltage limits remain undisclosed, so errors are reported in normalized units.

Reviewer_SXxEOpenReview ↗
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Paper summary

The paper introduces BatteryOCV, a paired measurement dataset and benchmark for reconstructing a slow diagnostic reference from fast measurements of the same battery cell. The dataset contains 404 industrial NCM/graphite cells from five anonymised product designs, with 1,894 measured low-rate references at 0.05C and 182,519 high-rate cycles at 0.33C or 0.5C. Each low-rate reference is indexed by physical cell and cycle and paired with a centred window of 64 neighbouring high-rate cycles from the same cell, so that the rate-to-reference mapping is supervised as the cell degrades.

The benchmark task takes a window of high-rate voltage profiles and predicts a 128-point low-rate voltage profile together with its charge and discharge capacities. Because the window is centred on the reference cycle, the task is retrospective. Evaluation is cell-disjoint and in two parts: a primary test on 370 held-out Model-E targets from 76 unseen cells, and a zero-shot test on 102 targets from 24 cells of four held-out designs A–D. Four metrics are reported: pooled profile RMSE, pooled capacity RMSE, a charge-branch-aligned RMSE, and a differential-voltage peak-count error.

The experimental comparison covers twelve classical controls: a constant training-target mean; four ways of reusing the high-rate observation directly, namely copying the centre cycle, its temporal mean, its temporal median, and a Savitzky–Golay smoothed copy; two fitted linear corrections, one pointwise affine and one current-based; four ridge variants on window voltage summaries, with and without observed capacity and in absolute and residual form; and nearest-neighbour retrieval. It further covers seven deterministic autoencoders and five generative models, each with one Optuna-selected configuration retrained over seeds 0, 1 and 42. On Model E, copying, temporal averaging and Savitzky–Golay smoothing all leave profile RMSE at about 0.0274, whereas ridge reaches 0.00429 and the best autoencoder 0.00362. On the held-out designs profile errors rise roughly threefold, and a supplementary study in which one or two cells per held-out design supply references shows that much of the resulting profile gain is matched by simply averaging those support references.

Critical strengths
  1. The dataset is the substantial part of the work. 404 industrial cells with 1,894 measured 0.05C references and 182,519 high-rate cycles, paired on the same physical cells and tracked across degradation, exceeds both the 8-cell Oxford characterisation set and the 94-cell paired C/5–C/40 reference-test set used in the closest published study by a factor of at least four. The pairing is done at the level of the physical cell and cycle index rather than by matching cells with similar histories, which is what makes direct supervision of the rate mapping possible at all, and the release includes the fixed split, the loader, the metrics and archived outputs for the tables it reproduces. The data being real, paired and documented is the one part of this submission I have no reservation about.

  2. The self-dissection is unusually honest, and it is what makes the negative results in the paper readable. The manuscript states, unprompted, that a constant curve with the right number of peaks scores perfectly on the peak-count metric, that providing both sides of the temporal context is no better than one side, that no window size is best on all metrics, that the comparisons carry no significance tests, and that the supplementary adaptation gain is largely a design-level prior rather than a learned mapping. The support-mean control in the supplementary study is the clearest instance: it is an input-independent baseline that the authors introduce against their own method, and it shows that an input-independent mean already reaches profile RMSE 0.00431 and 0.00427 with one and two support cells. What matters here is that most benchmark papers in this area do not report the control that most damages their own narrative, and it means the numbers in the paper can be trusted as reported even where the conclusions drawn from them cannot.

Both strengths concern the data and the reporting rather than the benchmark contribution, and I record them because they are real and because they mark what a re-positioned paper could build on. They are not a case for accepting this one.

Critical weaknesses

CW1. The benchmark evaluates a task that two cited papers already solve, and it evaluates neither of them.

  • Two published methods perform this reconstruction from far less input, at an accuracy the paper does not establish that it matches. Tian et al. (2021) reconstruct OCV–Q curves across the whole life from parts of a single 1C charge curve — concretely, charge amounts sampled at 5 mV steps over a 0.2 V window from 3.7 to 3.9 V, about forty numbers — and report RMSE of 7.9 mV on one cell with all eight cells within 10.8 mV, plus capacity error below 1%. Che et al. (2026) reconstruct C/40 curves from a single C/5 measurement and report a mean absolute voltage error below 3.4 mV across their three evaluation datasets, which span several aging protocols. Neither method is run here, and neither number appears anywhere in the submission.

  • The distinction the paper draws in Section 2.2 is about input requirements, not about whether the task is open. The text separates its own setting from prior work by observing that in BatteryOCV the full high-rate charge–discharge range is observed and the difficulty lies in the rate difference, whereas the cited methods address a missing part of the voltage range. That is not the correct axis: those methods take a high-rate measurement as input and produce a low-rate curve as output, so they face the rate difference as well, and they face it from substantially less data. The question the abstract poses — how much of a slow diagnostic reference can be recovered from fast measurements — is the question those papers answer.

  • The setting here is strictly more informative than either comparison, and the paper's own ablation shows that the extra information is not needed. The input is 64 complete high-rate charge–discharge cycles of 128 points, and the window spans 32 cycles before the reference plus the reference cycle and the 31 that follow, so 31 cycles after the target enter the input; the released loader confirms this indexing. Table 10 then shows that cutting the observation to the first, middle or last half of a single charge branch moves profile RMSE only from 0.00417 to 0.00452, 0.00653 and 0.00538. If half a branch suffices, the extra information this benchmark supplies is not what makes the reconstruction work; and since it supplies far more of it than either published method, it is measuring the easier version of the published problem.

  • The reported error cannot be placed against either published number, because its scale is withheld. Profile RMSE is computed on voltage normalised over a window whose limits Section 3.1 states are not disclosed, so the number is dimensionless. The manuscript's own Figure 5 nevertheless plots both the input and the output profile against a Voltage (V) axis running from 2.5 to 4.5 V, a span of exactly 2 V. If that axis is the normalisation window, then the reference configuration's 0.00358 corresponds to about 7.2 mV RMSE — the same order as Tian et al.'s 7.9 to 10.8 mV, obtained there from a two-hundred-millivolt slice of one curve. I am not asserting which method is more accurate across different cell chemistries; I am noting that the comparison is possible in principle, is the one a reader needs in order to interpret the paper, and is left impossible by a choice made in Section 3.1 while Figure 5 prints the numbers that would undo it.

  • The architecture table does not contain the paper's own best configuration, so it cannot be read as establishing where the state of the art lies. The reference configuration — Conv AE, voltage-only, segment bias and differential loss — is reported only in the component and input ablations, where it reaches 0.00358 profile, 0.01664 capacity and 0.00598 charge-aligned RMSE. Every one of the seven architectures in Table 4 is worse than that on all three of these metrics: the lowest profile and charge-aligned errors among them are Conv+LSTM at 0.00362 and 0.00615, and the lowest capacity error is Conv at 0.01787. Section 5.1 also describes the reference configuration as the setting of the architecture search, but the hyperparameters archived with the release show that six of the seven architectures were tuned to different loss weights, so the settings were not held fixed. A reader who wants to know how well a simple convolutional autoencoder does on this task has to assemble it from two tables, and the headline comparison sees the weaker of the two versions.

  • The consequence is that the paper's most quotable result is consistent with the opposite of its intended reading. The abstract reports that voltage-only ridge is competitive with the neural baselines, and Section 5.2.2 concludes that reconstruction therefore does not require a neural model. Against the numbers above, ridge's capacity RMSE of 0.01647 is in fact better than every architecture in Table 4 and better than the reference configuration as well, while its profile error sits between the models. Combined with the point above about input volume, the pattern — a linear model tying a deep one, a single cycle nearly tying sixty-four, and a published method matching the accuracy from a two-hundred-millivolt window — is the pattern one expects when the task is already easy, not when it is open. The paper does not argue that the task is hard, but it is presented as an open benchmark, and the evidence assembled here does not support that framing.

Taken together, the first weakness is not that the authors failed to engage with prior work: they cite the relevant papers and describe the methods above accurately. It is that a benchmark paper's central obligation is to establish that its task is not yet solved, and this one neither runs the methods that solve it nor reports its error in a unit that would allow the reader to see whether it is.

I want to be explicit that I do not see these as concerns a revision would clear. Adding the two missing methods would not repair the framing; it would test it, and the numbers already in the manuscript point to the outcome. Table 10 shows that replacing the full charge branch with its first half raises profile error by under a tenth, so a method that reaches the same error from forty charge values is not doing something harder. And the paper's own headline — a linear model matching the neural baselines — is what one expects when the mapping is close to linear over the observed range. What a revised manuscript could still deliver is the paired dataset and an honest statement that the rate gap on this data is largely recoverable by a linear map, with the cross-design capacity result reported as the negative finding it is. That would be a useful dataset paper. It is not the benchmark paper that was submitted, and the difference is not one of presentation.

References cited: Tian, Xiong, Shen & Sun, "Electrode ageing estimation and open circuit voltage reconstruction for lithium ion batteries", Energy Storage Materials 37:283–295, 2021; Che, Schaeffer, Rhyu, Wu, Asinger, Kim, Sass, Findeisen, Bazant, Chueh & Braatz, "Battery aging assessment: from critical insights to enhanced diagnosis", Energy & Environmental Science 19(6):1954–1968, 2026.

CW2. On the transfer setting the paper itself argues is the practically important one, the learned mapping does not carry over: on capacity it is worse than an input-independent constant in twelve of fourteen models, and the profile gain that the supplementary study reports does not hold across designs — it is carried by one of the four and reverses on two of the remaining three, so it is not evidence of a general improvement.

  • The capacity direction reverses on the held-out designs, and this is visible only by reading across three tables. Against a constant that predicts the Model-E training-target mean and uses no input at all, with capacity RMSE 0.02932 on A–D, the learned models are worse in twelve of fourteen cases: ridge 0.03854, Conv AE 0.03878, nearest-neighbour 0.03920, LSTM VAE 0.04002, Conv VAE 0.04130, Conv+LSTM 0.04313, MLP 0.05883, LSTM 0.07357, UNet 0.03379, Transformer AE 0.03447, Transformer VAE 0.03511, and diffusion 0.03549. Only Conv GAN at 0.02793 and BiLSTM at 0.02919 beat it. On profile error thirteen of the fourteen beat the constant, the exception being the diffusion model at 0.14428; so what transfers across designs is the shape of the curve and not its scale.

  • This matters because capacity is the quantity the task is defined to deliver, not a secondary diagnostic. Section 1 states that the two capacities are part of the target because shape alone does not give the capacity range on which voltage–capacity and DVA analyses are read, and Section 4.1 repeats that the profile grid does not determine the capacity scale. Section 6 then says that closing the cross-design gap matters because new designs are where slow references are scarcest. The reported result is that on those designs the capacity output is worse than a constant in twelve of fourteen models, which is the opposite of what the practical motivation requires.

  • The paper names one instance of this and not the others. Section 5.5 reports that MLP has the lowest held-out profile RMSE among the autoencoders but capacity RMSE 0.05883, against 0.02919 for BiLSTM and 0.02932 for the training-target mean. That is accurate, and it is the number the paper reports against its own case; but nearest-neighbour, ridge, Conv, Conv+LSTM, Transformer, LSTM, UNet, and four of the five generative models also exceed the constant in the same tables, and none of those crossings is mentioned. A reader who takes Section 5.5 at face value would conclude that one architecture has a capacity problem rather than that the capacity output does not transfer.

  • The aggregate that the supplementary study reports is carried by one of the four designs rather than shared across them. In Table 21, two-cell Conv adaptation reaches profile RMSE 0.00412 against 0.00427 for the input-independent support mean. Disaggregated, design A is worse than the support mean (0.00478 against 0.00374), design C is worse (0.00583 against 0.00494), design D is a tie (0.00447 against 0.00457), and the entire aggregate advantage comes from design B (0.00140 against 0.00374), which contributes 15 of the 102 targets and is the only held-out design measured entirely at 45 °C on the small capacity class. The paper is candid that the aggregate averages designs where adaptation helps with designs where it does not, and reports the ratio range from 0.36 on B to 1.27 on A, but it does not say that the sign of the aggregate is determined by B.

  • The two choices that define the benchmark are selected on the metric the paper itself downgrades. Segment bias and differential loss are adopted because together they take peak-count error from 0.133 to 0.086; in the same ablation, profile error moves by 0.00004 within one standard deviation, charge-aligned error is unchanged to five decimals, and capacity error gets worse, from 0.01561 to 0.01664. The default window length of 64 is likewise adopted over 16 only on peak-count error, 0.133 against 0.280, on a cell whose standard deviation is 59% of its mean. Section 5.3 has already told the reader that a constant curve with the right number of peaks scores well on this metric. So the reference configuration and the default window both rest on the one metric the paper describes as a coarse check.

  • The three ablations that establish those choices are not reproducible from the released package. The package ships the split, the loader, the metrics, the twelve classical controls, the seven deterministic and five generative architectures, and the archived outputs for the context, boundary, partial-observation, architecture and generative tables. It contains no script and no archived output for the window ablation, the component ablation, or the input ablation: the runner exposes only the split, inspect, baselines and single-configuration commands, the experiments directory has no script for them, and a search of the package for the relevant terms returns nothing. These are precisely the three tables on which the reference configuration, the default window length and the shape-versus-scale argument rest.

Taken together, the failure is not a tuning detail. On the transfer case that motivates the paper, the capacity output is worse than a constant in twelve of fourteen learned models — the benchmark therefore fails in the direction that decides whether it is useful — and the one supplementary aggregate that looks favourable is carried by a design contributing 15 of the 102 targets. The two settings that define the benchmark are both chosen on the metric the paper itself calls a coarse check, and the table that justifies the component choice also records its cost, capacity error rising from 0.01561 to 0.01664. And the three ablations behind those settings have neither script nor archived output in the release. A benchmark whose motivating case fails, whose defaults rest on a downgraded metric, and whose supporting ablations cannot be checked does not establish the protocol it proposes.

Questions for authors
  1. Would the authors run Tian et al. (2021) and Che et al. (2026) on this benchmark, or report where their reported errors cannot be reproduced under this protocol? This is the question that most affects my assessment. The two methods take high-rate measurements as input and produce low-rate curves, at 7.9–10.8 mV RMSE and below 3.4 mV mean absolute error respectively, and a comparison under this paper's protocol would establish both whether the task is open and where the baselines sit.

  2. Is the 2.5–4.5 V axis that Figure 5 draws on both its input and its output panel the normalisation window whose limits Section 3.1 describes as not disclosed? If so, profile RMSE can be converted to millivolts — 0.00358 becoming about 7.2 mV — and the comparison above becomes possible without any new experiment. If not, could the authors state the window, or report profile error in millivolts alongside the dimensionless value?

  3. Why is the reference configuration not a row in Table 4, given that it reaches 0.00358, 0.01664 and 0.00598 on the profile, capacity and charge-aligned metrics, better on all three than every architecture listed there? Related clarification: Section 5.1 describes this configuration as the setting of the architecture search, while the archived hyperparameters show different loss weights for six of the seven models. Which of the two is the intended reading?

  4. Could the authors release the scripts or archived outputs for the window, component and input ablations? Without them the reference configuration and the default window length cannot be checked from the package, and those two choices determine every other number in the paper.

  5. For the charge-aligned metric, how many targets were excluded because the common capacity interval was not positive? The evaluator returns an undefined value in that case and the mean is taken over the remaining targets, so the exclusion is currently invisible.

  6. Two minor clarifications, neither of which affects my recommendation on its own. First: Section 3.1 says the benchmark uses only high-rate voltage as input, whereas Table 16 evaluates temperature, current and observed capacity as additional inputs — is that sentence meant to describe the reference configuration rather than the benchmark as a whole? Second: the README's example command for the partial-observation experiment passes four of the five conditions reported in Table 10 — is that example meant to be a complete invocation?

References cited: Tian, Xiong, Shen & Sun, "Electrode ageing estimation and open circuit voltage reconstruction for lithium ion batteries", Energy Storage Materials 37:283–295, 2021; Che, Schaeffer, Rhyu, Wu, Asinger, Kim, Sass, Findeisen, Bazant, Chueh & Braatz, "Battery aging assessment: from critical insights to enhanced diagnosis", Energy & Environmental Science 19(6):1954–1968, 2026.

2 comments
AuthorsOpenReview ↗

Response to Reviewer SXxE (1/2)

1. Tian/Che and the benchmark contribution. Tian et al. and Che et al. address related high-to-low-rate reconstruction problems. BatteryOCV's primary contribution is not to introduce high-to-low-rate reconstruction as a new problem, but to provide repeated, physically paired high- and low-rate measurements together with a common, cell-disjoint evaluation protocol. This enables separate assessment of profile reconstruction, capacity estimation, longitudinal changes, and generalization to unseen product designs.

Consequently, reconstruction accuracy reported by prior studies under different experimental conditions does not, by itself, establish performance or generalization under these evaluation settings.

Tian uses electrode-reference-based characterization to define electrode aging targets and reconstruct OCV from predicted electrode states. Its evaluation uses cells from the same Oxford product. Che uses measured electrode OCP references and fits electrode states to C/40 curves before residual correction; Dataset 3 trains and tests its residual model within that product. BatteryOCV instead evaluates direct reconstruction from full-cell cycling records, without electrode-reference curves or fitted electrode-state parameters.

We have not evaluated either method on BatteryOCV, which lacks matched electrode references for A–E. Their reported mV errors come from different fitting and testing protocols, not our cell-disjoint benchmark. In particular, Tian's quoted 7.9–10.8 mV describes offline fitting, not end-to-end measured-reference error.

The held-out A–D results separate shape from capacity:

Comparison with training-target constantLearned methods
Lower profile RMSE13 / 14
Higher capacity RMSE12 / 14

Profile shape alone does not preserve capacity scale. With observed high-rate capacity as input, fixed Conv's A–D capacity RMSE falls from 0.051238 to 0.020189. The benchmark measures these distinct outcomes using repeated low-rate references from the same physical cells.

References: Tian, Che, Che SI.

2. Figure 5 and voltage units. Figure 5 is an illustrative schematic, not measured curves or predictions. Its 2.5–4.5 V axes were mislabeled; the revision will use normalized illustrative axes. These endpoints are not the normalization limits. The physical voltage window is proprietary, so the normalized RMSE cannot be converted to mV from Figure 5.

3. Reference Conv and tuning settings. The reference Conv should have been included in Table 4. The paper also needs to distinguish common architecture components from architecture-specific tuned loss weights. Below are three-seed, cell-macro results on the fixed split, separate from the original pooled results:

Test setMethodProfile RMSECapacity RMSEPenalized peak
EFixed Conv0.0027240.0138400.011825
ESelected Conv, early stop0.0101950.0192750.019394
ESelected Conv, full budget0.0028680.0139430.012349
ERidge0.0034640.0132590.009161
A–DFixed Conv0.0099010.0512380.025974
A–DSelected Conv, early stop0.0184240.0230800.021286
A–DSelected Conv, full budget0.0104260.0302940.024426
A–DRidge0.0106480.0307490.020272

E has 76 cells/370 references; A–D has 24/102. Selected Conv is trial 19 from the archived-candidate replay. Ridge is better than both Conv settings on E capacity and peak error; the selected model is also sensitive to the training budget.

AuthorsOpenReview ↗

Response to Reviewer SXxE (2/2)

4. Ablations and transfer results. The original supplementary package lacked archived outputs for the window, component and input ablations. The supplementary ZIP accompanying this response contains the shared runner, configurations, keyed predictions, evaluation code and table-generation scripts for 69 completed runs (23 settings × three seeds).

Adding observed high-rate capacity to fixed Conv reduces capacity error in each held-out design. No target-design low-rate references enter training:

DesignCells / referencesVoltage-only capacity RMSE+ high-rate capacityDifference [95% CI]
A8 / 400.0342710.024358−0.009913 [−0.013117, −0.006492]
B7 / 150.0176860.009487−0.008199 [−0.008781, −0.007503]
C4 / 170.0962820.024443−0.071839 [−0.076766, −0.066653]
D5 / 300.0893210.025096−0.064225 [−0.072278, −0.056591]

Metrics average seeds, references within each cell, then cells. Intervals use 5,000 paired cell bootstrap resamples. C/D account for approximately 82% of the aggregate improvement. With only 4–8 cells per product, these intervals describe observed-cell uncertainty, not uncertainty across future designs. Auxiliary high-rate capacity does not improve A–D successive-profile-change error over a zero-change baseline. In the original comparisons, 12/14 learned methods still lose to the constant on held-out capacity. The aggregate two-cell adaptation profile gain over the support mean is largely driven by B.

These findings highlight that accurate profile reconstruction does not necessarily translate into accurate capacity estimation, and that the benefits of few-cell adaptation can vary substantially across product designs. They underscore the importance of evaluating profile and capacity performance separately, with design-level reporting and comparisons against simple, input-independent baselines.

For the new peak metric, we tested nine combinations of matching distance and unmatched-peak penalty (0.025, 0.05, 0.10 each). On E, original Conv and Ridge beat the mean throughout. On A–D, original Conv versus the mean remains inconclusive, with one point-ranking reversal.

W64 is a reference context, not an accuracy optimum. With segment bias and differential loss disabled:

Context windowE peak errorA–D peak error
W10.0123230.022663
W640.0129170.028456

The centered window includes post-reference cycles, so the task is retrospective, not past-only forecasting.

5. Charge-aligned exclusions. No targets were excluded for nonpositive common capacity overlap in the earlier 98 audited evaluations or the new 138 E/A–D evaluations (370 E and 102 A–D references per run).

6. Documentation and release. “Voltage-only” describes the reference setting, not all permitted inputs. The corrected README lists all five partial-observation conditions. The accompanying code archive includes an MIT license. The normalized HDF5 and fixed splits remain available via the anonymous review link. Dataset license terms and a permanent URL remain pending. Proprietary voltage limits and raw-to-HDF5 processing are not included.

Reviewer_YDNGOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
1
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Paper summary

BatteryOCV pairs high-rate cycling data with low-rate reference measurements from 404 battery cells across five product designs. The task is to reconstruct low-rate voltage curves and capacities from nearby high-rate cycles. The paper compares classical and neural baselines using cell-disjoint splits. Learned models improve reconstruction within the main design, although ridge regression is competitive with the neural models. Performance drops substantially on unseen designs, and a simple design-specific mean explains much of the profile improvement obtained through adaptation.

Critical strengths
  • The repeated high-rate and low-rate measurements on the same cells are a useful resource. They provide direct supervision across aging stages, and the cell-disjoint splits make the evaluation more credible.

  • The simple baselines are well chosen. Including constant predictions, ridge regression, and retrieval gives a clearer picture of what the neural models contribute. Evaluating capacity separately from curve shape is also helpful.

Critical weaknesses

It remains unclear whether the reconstructed curves preserve useful diagnostic information. The main local-feature metric only counts peaks. A constant prediction achieves zero peak-count error on the held-out designs (Table 5), despite having substantial profile error. Peak locations and spacing matter to the paper’s motivation, but their reconstruction accuracy is not quantitatively established. The authors acknowledge this limitation, yet acknowledging it does not resolve the evaluation gap. The flawed peak-position metric was also retained in hyperparameter selection, without checking whether correcting it changes the conclusions.

The benchmark’s broader value is not sufficiently demonstrated. Of the 404 cells, 380 come from one design. The remaining four designs contain only 24 cells and cover relatively limited degradation. In the adaptation experiment, simply averaging the references from two support cells gives profile RMSE 0.00427, almost matching the adapted Conv AE at 0.00412 (Table 21). Capacity prediction does improve, but these results leave open how much cell-specific aging information is recovered beyond a typical curve for each design. I would need stronger evidence on this point to view the benchmark as a substantial contribution.

Questions for authors
  • How accurately do the models recover peak locations, spacing, and changes across aging stages compared with the constant and support-mean baselines? An evaluation should account for missing and extra peaks.

  • Do the main conclusions hold when hyperparameter selection excludes or corrects the flawed peak-position metric?

  • Can you evaluate changes between successive reference measurements within each cell? This would help distinguish recovery of aging-related changes from prediction of a design-specific average.

3 comments
AuthorsOpenReview ↗

Response to Reviewer YDNG

1. Local features versus mean baselines. We supplement peak count with one-to-one matching of peak positions and penalties for missing/extra peaks (distance and penalty both 0.05 on normalized capacity axes). The results are:

MethodE peak errorE spacing MAE (eligible refs)A–D peak error
Training mean0.0198670.013947 (365)0.021411
Ridge0.0091610.008804 (370)0.020272
Original Conv0.0120080.013589 (370)0.020045

E has 76 cells/370 references and A–D 24/102. Conv improves over the mean on E, but not clearly on A–D; Ridge has the lowest E feature errors.

In two-cell adaptation, the support mean uses low-rate references from two target-design cells separate from the query cells. On 23 query cells (99 unique references), support mean/Conv peak errors are 0.009883/0.011978, with a paired difference CI including zero. Original Table 21 reports profile RMSE 0.00427/0.00412 and capacity RMSE 0.02138/0.01446, averaged over 12 support selections; those aggregates use a different weighting scheme.

2. Does the peak metric affect selection? Peak terms rank configurations, not weights or checkpoints; checkpoint selection uses validation profile RMSE. Re-ranking the 20 archived Conv candidates under six scoring criteria consistently selected trial 19. However, fresh TPE searches with and without peak-related terms selected different configurations. This indicates that hyperparameter search outcomes can be sensitive to the selection objective, rather than demonstrating instability in the ranking of the existing candidates. Both configurations from the fresh searches were refitted with three seeds before test evaluation. The accompanying supplementary ZIP includes the search configurations, saved predictions and evaluation scripts.

Test setSelection scoreProfile RMSECapacity RMSEPenalized peak
EOriginal0.0026950.0137490.012085
EPeak-free0.0027440.0138600.011934
A–DOriginal0.0088670.0376880.021374
A–DPeak-free0.0088000.0476330.027802

Peak-free selection increases A–D capacity error by 0.009945 (95% paired cell-bootstrap CI [0.003768, 0.015974]) and peak error by 0.006428 [0.004742, 0.008139]. E differences and the A–D profile difference are inconclusive. The main in-design advantage and cross-design gap persist, although configuration selection affects OOD capacity and peaks.

3. Changes across aging stages. We compared measured and predicted changes between consecutive low-rate profiles of each test cell:

\Delta\hat y_{c,k}=\hat y_{c,k+1}-\hat y_{c,k}.$$ We report RMSE between $\Delta y$ and $\Delta\hat y$. A fixed mean predicts zero change. | Test set | Cells / consecutive pairs | Zero-change RMSE | Original Conv RMSE | | --- | --- | ---: | ---: | | E | 76 / 294 | 0.005106 | 0.003495 | | A–D | 24 / 78 | 0.003780 | 0.005022 | On E the Conv-minus-control difference is −0.001611 (95% paired cell-bootstrap CI [−0.002202, −0.001037]); on A–D Conv is worse. Thus the model tracks some within-cell change on E but not reliably on new designs. All data splits are cell-disjoint, and bootstrap resampling keeps repeated references within their cells.

The rebuttal is helpful and addresses some of my questions, but it does not resolve my central concerns about this paper’s generalization and the advantage of its method over simple design-level baselines. I therefore maintain my original rating.

AuthorsOpenReview ↗

Response to Reviewer YDNG

Thank you for your follow-up. We would like to clarify two points.

First, the two-cell support mean is a strong baseline, but it requires measured low-rate references from the target design. Unlike our zero-shot evaluation, it uses target-design information. We therefore compare it with adapted Conv under the same few-shot setting, separately from the zero-shot results.

Second, our task reconstructs both the normalized voltage profile and its charge and discharge capacities. A mean curve may capture the typical profile shape without recovering individual-cell capacity. In Table 21, the support mean and adapted Conv achieve similar profile RMSEs (0.004270.00427 vs. 0.004120.00412), but differ more in capacity RMSE (0.021380.02138 vs. 0.014460.01446). This does not establish a general advantage for neural models, but shows why profile error alone is insufficient.

BatteryOCV evaluates both aspects and reveals that good within-design reconstruction does not necessarily transfer to unseen designs. Its contribution is the paired dataset and benchmark that make these differences measurable, rather than a model that has already solved cross-design generalization.

Reviewer_W5mtOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

BatteryOCV introduces a paired dataset and benchmark for reconstructing measured low-rate voltage profiles and charge and discharge capacities from high-rate cycling data. It contains repeated measurements from 404 industrial cells across five product designs. The benchmark evaluates unseen cells from the training design and zero-shot transfer to four held-out designs. Ridge regression is competitive with neural baselines within the training design, while profile errors increase on held-out designs.

Critical strengths

Repeated high- and low-rate measurements on the same physical cells allow reconstruction to be evaluated against measured references at multiple stages of degradation. The benchmark also includes strong classical controls. On the Model E test set, voltage-only ridge reduces profile RMSE from 0.02746 for the high-rate identity baseline to 0.00429.

Critical weaknesses

The peak-count metric provides limited evidence that diagnostically relevant local features are recovered. In Table 5, the training-target mean achieves zero peak-count error on held-out designs despite a profile RMSE of 0.01774. Could the authors compare against this control using a metric that captures peak displacement and penalizes missing and spurious peaks?

The held-out-design evaluation demonstrates a transfer gap, but its causes are difficult to separate. The evaluation covers 24 cells, and product design, operating conditions, and degradation coverage vary together. Where sample sizes permit, how much of the gap persists within overlapping operating conditions and degradation ranges?

Questions for authors
  1. In Table 5, the training-target mean has zero peak-count error on held-out designs. Can the authors compare methods using a metric that measures peak displacement and penalizes missed and spurious peaks?

  2. Where sample sizes permit, how much of the held-out-design performance gap persists among cells with overlapping operating conditions and degradation ranges?

3 comments
AuthorsOpenReview ↗

Response to Reviewer W5mt

1. Peak displacement and missing/extra peaks. Peak count cannot distinguish correctly placed peaks from displaced or missing peaks. We re-evaluated saved predictions using one-to-one matching: matched peaks contribute positional error and unmatched peaks incur a penalty. We average charge and discharge scores using the metric below:

\frac{\sum_{(i,j)\in M}|t_i-p_j|+\lambda(|T|+|P|-2|M|)}{|T|+|P|-|M|}.$$ Here $T$ and $P$ are reference and predicted peak positions; $M$ is a one-to-one matching within distance $\tau=0.05$. Each unmatched peak incurs penalty $\lambda=0.05$ (normalized capacity coordinates). The A–D results (24 cells, 102 references) illustrate the difference: | Method | Peak-count error | Penalized peak error | | --- | ---: | ---: | | Training-target mean | 0.00000 | 0.021411 | | 1-NN retrieval | 0.00000 | 0.017824 | | Transformer | 0.00000 | 0.016967 | | Ridge | 0.01354 | 0.020272 | | Original Conv | 0.13094 | 0.020045 | Across nine distance/penalty combinations (0.025, 0.05, 0.10 each), Conv and Ridge beat the E mean with paired confidence intervals below zero. On A–D, Conv versus the mean is inconclusive in all nine; their point ranking reverses once. The accompanying supplementary ZIP includes these evaluations. **2. Product-held-out evaluation.** Model E training already covers 25/45°C and 0.33/0.5C. Thus A–D test held-out product designs, not separately unseen temperatures or C-rates. We compared each design against E within common temperature/rate strata and overlapping capacity-retention ranges, using common stratum weights. | OOD − E | E cells / references | OOD cells / references | Capacity RMSE gap | Peak-error gap [95% CI] | | --- | --- | --- | ---: | --- | | A − E | 65 / 155 | 8 / 39 | +0.017152 | +0.009267 [0.007081, 0.011098] | | B − E | 41 / 76 | 7 / 15 | +0.002192 | +0.003140 [0.002021, 0.004308] | | C − E | 64 / 139 | 4 / 16 | +0.033611 | +0.013047 [0.011636, 0.015294] | | D − E | 65 / 163 | 5 / 28 | +0.017349 | +0.009904 [0.006740, 0.013322] | | All A–D − E | 65 / 204 | 24 / 100 | +0.017088 | +0.008545 [0.006726, 0.010293] | Positive gaps mean worse OOD performance. Intervals use 2,000 whole-cell bootstrap resamples; E subsets vary with the overlapping conditions. B shares E's small-capacity class and has the smallest matched gaps, but its aging coverage and other design properties also differ. The observed association does not isolate a capacity-class effect.

We thank the authors for the additional analysis.

The penalized peak error addresses our concern about peak count. It shows that Conv and Ridge beat the training-target mean on Model E, while the comparison on A–D is inconclusive. Please state this in the paper.

The matched comparison shows the held-out gap remains under common operating conditions and degradation ranges. Reporting the same gap for profile RMSE would help.

Our concerns are largely addressed. We keep our rating.

AuthorsOpenReview ↗

Response to Reviewer W5mt

Thank you for your follow-up.

1. Peak-error interpretation.

We will clarify in the revised manuscript that Conv and Ridge outperform the training-target mean on Model E under the penalized peak metric, while the differences on A–D remain inconclusive (main-text Table 2 and Appendix Table 9).

2. Matched profile RMSE.

Using the same Conv predictions, matched operating conditions and degradation ranges, and cell-level bootstrap procedure as in our previous response, we obtain:

ComparisonE cells / refsOOD cells / refsProfile RMSE gap [95% CI]
A − E65 / 1558 / 39+0.006707 [0.006138, 0.007170]
B − E41 / 767 / 15+0.005911 [0.005088, 0.006614]
C − E64 / 1394 / 16+0.009628 [0.008056, 0.012101]
D − E65 / 1635 / 28+0.009664 [0.009132, 0.010346]
All A–D − E65 / 20424 / 100+0.007639 [0.006803, 0.008502]

The profile RMSE gap remains positive for all four held-out designs after matching operating conditions and degradation ranges. Thus, the transfer gap is not explained solely by the observed differences in these conditions.

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

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