CW1. The benchmark evaluates a task that two cited papers already solve, and it evaluates neither of them.
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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.
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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.
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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.
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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.
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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.
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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.
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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.
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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.
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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.
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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.
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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.
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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.
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:
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}.
Slope error is reported in normalized capacity per 100 cycles:
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.