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Paper summary
This paper proposes an approach for reconstructing daily global XCO2 fields from sparse OCO-2 retrievals. The central idea is to give the model some background knowledge about CO₂ using a language model. More specifically, the authors ask a language model (they never say which one) a set of simple questions. For each pair of climate zone and vegetation type, they ask how much CO₂ the plants there usually take up and how much the ecosystem gives off. They also ask how much CO₂ human activity adds at each emission level, and how these effects change with the seasons for each vegetation type. The answers are saved as fixed scores in lookup tables, mapped to pixel-wise fields, and injected into a Mamba backbone through a gated residual knowledge adapter.
Critical strengths
- The paper tackles an important problem and clearly lays out the data choices (Sections 3, 5.1, Appendix A). The goal is a daily CO₂ map at fine resolution, covering both land and ocean, with no gaps. The model is trained on sparse OCO-2 satellite readings, uses CAMS as the background estimate, and holds out the TCCON ground stations as an independent check.
- The LLM is used only once to build the priors, so training and inference stay cheap and deterministic. The authors also do not claim the LLM scores are real measurements of how much CO₂ is taken up or released.
- Modeling the residual over CAMS, with regularizers on the residual rather than on absolute XCO2 (Eqs. S3-S5), is interesting.
- The discussion is candid. Section 7 states the prior branch gives a measurable but moderate accuracy gain and frames the result mostly as optimization guidance.
- Table 3 reports per-site TCCON numbers, including the weak sites (Eureka and Xianghe with RMSE above 1.7 ppm, JPL with R² of 0.69), rather than only an aggregate.
Critical weaknesses
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The central claim, that LLM-based priors add useful knowledge, is not separated from a simpler explanation. The priors are a fixed lookup (on climate zone, vegetation type, emission level, and season), and may just be better at re-encoding categorical inputs. Any network given those categories could implicitly learn an equivalent table from data. While the authors use these categories to build the prior tables, it is not clear if the knowledge-free Mamba could also benefit by just including these categories as extra input variables. The emission level also likely comes from ODIAC, which is already an input. To support the key claim of the paper, it is important to incude: (a) the knowledge-free backbone given the same categories as learned embeddings; (b) the same adapter fed random or shuffled prior tables; (c) the adapter fed priors from the literature (e.g., CarbonTracker).
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The paper does not provide enough detail to reproduce it. For the LLM, it never names the model or shares the prompts, the number of samples, the category lists or the final tables. That is a real gap, since the priors are the main contribution. The knowledge adapter is not clearly described. Basic training details are also missing: model size, optimizer, learning rate, loss weights, compute and training time. The prior tables, and how much they vary across LLM runs and across LLMs, should go in the appendix.
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The accuracy gains are very small and come from single runs with no variance reported. Removing the prior branch moves held-out MSE from 0.658 to 0.671 and R² from 0.925 to 0.923 (Table 1). Removing the 0.25° branch moves R² by 0.001. The improvement over Trans-XCO2 is 0.811 vs 0.836 ppm RMSE. These differences could easily be within seed variation. The convergence claim (Figure 3) rests on one noisy validation curve per model. Results over several seeds, with mean and standard deviation, are needed before the ablation can be read as evidence.
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Table 2 and Figure 2 seem to cover the full 2018-2020 period rather than only the held-out dates. If so, part of that data was used for training, which would explain why the error there is lower (0.77 vs 0.811 ppm). Can the authors confirm which dates Table 2 uses? If training dates are included, the 0.77 score should not be used to compare against other methods.
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The data split is underspecified. Section 5.1 and Appendix C say only date-based split. The paper should give the fraction of held-out dates, whether they are random or in contiguous blocks, and whether validation and test dates are distinct. XCO2 could be strongly correlated across adjacent days, and CAMS is an input on every day, so randomly scattered held-out days give an optimistic estimate. A blocked split would be more convincing.
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The 0.05° claim is not clearly supported. Every input is resampled to 0.25° (Table S1), even ODIAC and MODIS, which exist at 1 km. So the model has no fine-scale inputs to work with. The global maps in Figures 4-5 cannot show the difference between 0.05° and 0.25°. A comparison against the 0.25° output simply upsampled to 0.05°, plus zoomed maps over cities, would show whether any real fine detail is recovered.
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Table 3 reports only GeoPrior-Mamba. Site-level R² on daily XCO2 is driven mostly by the seasonal cycle and the yearly trend, which CAMS already captures well, so R² above 0.9 is not surprising. CAMS and Trans-XCO2 should be evaluated against TCCON with the same collocation rule.
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Trans-XCO2 is the only learned baseline reported. Simple baselines on the same inputs would show where the Mamba model really stands, for example kriging, a U-Net, or a gradient-boosting model.
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Some citations in Table S2 do not match the papers they point to. For example, Qu et al. (2026) is listed as DINEOF-BME, but that paper uses a Transformer-BiLSTM. Huang et al. (2024) is listed as a global 1° method, but that paper covers only China.
Questions for authors
- Does the knowledge-free Mamba baseline receive climate zone, vegetation type, and emission level as inputs? If not, can you report a variant where these categories are given as learned embeddings, so that the only difference is whether the table values come from the LLM or are learned?
- What happens if you replace the LLM tables with random, shuffled, or constant values? If performance is similar, the gain comes from the adapter, not from the knowledge.
- Which language model did you use, with what prompts, and how many responses per combination? How much do the tables differ across LLMs, and how sensitive are the results to that choice? Can you include the final prior tables?
- How were held-out dates chosen (fraction, random vs blocked)? Are validation and test dates disjoint? How do the results change under a blocked split (e.g., train on 2018-2019, test on 2020)?
- Is Table 2 computed over all dates, including training dates? If so, why is its 0.77 ppm used in Table S2?
- Can you report mean and standard deviation over multiple seeds for every row of Table 1, and for the convergence comparison in Figure 3?
- How do CAMS and Trans-XCO2 compare against TCCON under the same collocation as Table 3?
- What evidence is there that the 0.05° output contains real structure below 0.25°, given that all inputs are at 0.25°? How does it compare to upsampling your own 0.25° output?
- Is the predicted log-variance calibrated? For example, what fraction of held-out OCO-2 observations fall within the predicted 1σ and 2σ intervals?
- Table S2 lists Trans-XCO2 for 2021-2024. Did you retrain it on 2018-2020 with comparable tuning effort, and how do the two models compare in parameter count and training cost?
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Post-Rebuttal Comments
Thank you for the detailed response and for narrowing the claims on resolution, TCCON and calibration. Unfortunately, I am not able to raise my score, because my main concerns remain:
- Limited novelty and I have concerns regarding the significance of the results. The learnable-table control is useful, but its 1.5% gain is on the validation set, without standard deviations, and the permuted-prior and multi-seed results are not yet available.
- Reproducibility. The prompts, prior tables, adapter details and training settings are still to be released.
- Baselines. Trans-XCO2 is still the only learned baseline, and TCCON has no comparison with CAMS or Trans-XCO2.
Q1. Knowledge-free inputs and matched control. The knowledge-free model does not receive climate-zone, vegetation-type, emission-level, or seasonal-prior IDs, but retains ODIAC and NDVI/EVI. Removing the prior pathway increased held-out test MSE from 0.658 to 0.671 ppm². We also retained the same indices, table structure, adapter, backbone, and training settings, while replacing the fixed prior with 309 randomly initialized learnable coefficients. Across training seeds, the DeepSeek prior achieved a mean best-validation MSE of 0.6284 versus 0.6380 for this control (1.5% lower). This suggests that its values contribute beyond the table structure and adapter capacity. We will report standard deviations and seed IDs.
Q2. Learnable-table and permuted-prior controls. The randomly initialized learnable-table control tests whether reconstruction training alone can learn suitable coefficients using the same categorical structure and adapter. Its higher validation MSE (0.6380 versus 0.6284) supports a contribution from the fixed elicited values. The frozen permuted-prior control suggested by the reviewer is still running at the rebuttal deadline; therefore, we do not report its result here. We will include the result in the revised manuscript once completed.
Q3. LLM and reproducibility. The original prior was generated with DeepSeek-V4-Pro (thinking disabled, temperature 0.8,
max_tokens=6000). For each elicitation unit, five outputs (seeds 1001–1005) were aggregated by element-wise median. Each sample used 20 primary calls: 8 climate tables, 10 seasonal tables, 1 evergreen override, and 1 emission table. The tables were fixed before training; no LLM is used during training or inference. Using the same procedure, a GPT-5 prior obtained approximately 0.630 mean best-validation MSE versus 0.6284 for DeepSeek. This indicates broadly similar downstream performance, not statistical equivalence; prompt sensitivity remains untested. We will release the prompts, settings, constraints, and tables in NPZ and CSV/JSON formats.Q4. Date split. After excluding two dates needed for historical inputs, 1,094 dates from 2018–2020 were shuffled by date with seed 42 into 765/164/165 train/validation/test dates (approximately 70/15/15). All observations from one date remain in one subset, and validation and test dates are disjoint. Because these subsets are temporally interleaved, this tests unseen dates within 2018–2020, not future-year generalization. A blocked split has not been completed, and we make no claim under stronger temporal shift.
Q5. Table 2. Figure 2 and Table 2 cover the full 2018–2020 period and include training dates. Their 0.77 ppm RMSE is descriptive, not held-out performance. We will clarify this and use the held-out Table 1 RMSE of 0.811 ppm for comparisons.
Q6. Multiple seeds. Each seed is an independent run. We select its checkpoint by validation MSE and evaluate it once on the held-out test set. We will report mean ± standard deviation and seed IDs. Figure 3 shows representative trajectories; revised tables will aggregate independent runs.
Q7. TCCON comparisons. Table 3 is an external ground-based consistency assessment, not a comparative benchmark. Without CAMS, Trans-XCO₂, and knowledge-free outputs evaluated under identical collocation and quality control, it cannot establish relative improvement. We will replace “independent validation” with “external ground-based consistency evaluation” and limit its interpretation accordingly.
Q8. Meaning of 0.05°. All predictors enter at 0.25°; coarse and fine decoders produce 0.25° and 0.05° outputs. Thus, 0.05° denotes output-grid spacing and target-supervision scale, not native information below 0.25°. Removing the coarse branch increased test MSE from 0.658 to 0.664 ppm², supporting multi-scale supervision but not superiority over an upsampled 0.25° output. We will narrow the claim accordingly.
Q9. Log-variance calibration. The log-variance head is trained with Gaussian NLL as an uncertainty-aware objective. We have not tested interval calibration and make no calibration claim. Removing NLL increased test MSE from 0.658 to 0.666 ppm², demonstrating optimization/regularization utility only. Future work will examine 1σ/2σ coverage and reliability diagrams.
Q10. Trans-XCO₂. We retrained Trans-XCO₂ on the same 2018–2020 data, split, and held-out OCO-2 mask. Its test RMSE was 0.836 ppm versus 0.811 ppm for GeoPrior-Mamba. We will report settings, parameter counts, hardware, wall-clock time, and inference cost. The public 2021–2024 result in Table S2 is distinct from this retrained baseline.
We will also correct the Qu et al. and Huang et al. descriptions, audit Table S2 citations, and avoid claiming universal superiority over convolutional models without a matched baseline.