acceptodds
Under review as a conference paper at ICLR 2027

GeoPrior-Mamba: Structured Process Priors with Mamba for Fine-Resolution XCO2 Reconstruction

Abstract

Reconstructing fine-resolution column-averaged dry-air CO2 (XCO2) fields from sparse satellite observations requires models to infer spatial structure that is only weakly constrained by direct measurements. Existing learning-based methods typically treat environmental covariates as ordinary numerical inputs and must therefore learn heterogeneous source-sink relationships largely from sparse supervision. We introduce GeoPrior-Mamba, a multi-directional Mamba framework augmented with offline language-model-induced structured process priors. Rather than using a language model to predict XCO2, we use it before training to organize relative process knowledge for biospheric uptake, ecosystem respiration, and anthropogenic emissions into deterministic prior tables. These priors are spatially instantiated using geographic, ecological, emission-related, and seasonal information and are adaptively injected into the reconstruction backbone through a lightweight knowledge adapter. Using OCO-2 observations from 2018-2020, GeoPrior-Mamba achieves an RMSE of 0.81 ppm and an of 0.93 on held-out observations, reducing RMSE by 48.2% relative to CAMS background interpolation and by 3.1% relative to Trans-XCO2 under the same evaluation protocol. Ablation experiments show a measurable contribution from the knowledge-prior branch and substantially faster convergence than the knowledge-free Mamba backbone. Independent TCCON evaluation further supports the consistency of the reconstructed fields with ground-based column CO2 measurements. These results suggest that language models can provide a practical mechanism for constructing structured process priors when globally consistent process-response representations are difficult to obtain directly, while remaining outside the numerical prediction loop.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
Language-Model-Induced Priors, State Space Models, XCO2 Reconstruction, Satellite remote sensing

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_eQh7OpenReview ↗
Rating
1
Confidence
2
Informativeness
2
Presentation
2
Soundness
1
Read review
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
  • 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).

  • 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.

  • 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.

  • 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.

  • 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.

  • 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.

  • 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.

  • 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.

  • 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
  1. 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?
  2. 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.
  3. 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?
  4. 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)?
  5. Is Table 2 computed over all dates, including training dates? If so, why is its 0.77 ppm used in Table S2?
  6. Can you report mean and standard deviation over multiple seeds for every row of Table 1, and for the convergence comparison in Figure 3?
  7. How do CAMS and Trans-XCO2 compare against TCCON under the same collocation as Table 3?
  8. 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?
  9. Is the predicted log-variance calibrated? For example, what fraction of held-out OCO-2 observations fall within the predicted 1σ and 2σ intervals?
  10. 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?
2 comments

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.

Reviewer_eQh7OpenReview ↗

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.
Reviewer_eJFxOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

GeoPrior-Mamba reconstructs daily 0.05° XCO2XCO_2 residuals relative to the CAMS background field using 0.25° environmental covariates and sparse OCO-2 retrievals from 2018 to 2020. The model queries a language model offline to generate fixed relative-activity priors for biospheric uptake, ecosystem respiration, and anthropogenic emissions. These instantiated spatial priors are injected into a multi-directional Mamba backbone via a knowledge adapter. On the held-out test set, the model achieves an RMSE of 0.811 ppm, compared to 0.836 ppm for Trans-XCO2XCO_2 and 1.565 ppm for CAMS interpolation. Removing the knowledge branch raises the MSE from 0.658 to 0.671

Critical strengths
  1. The LLM is used only offline, to build small fixed tables using repeated sampling, sanity screening and median aggregation. Training and inference therefore stay deterministic and cheap, and the priors can be inspected and edited. Separating knowledge elicitation from numerical prediction is a sensible design for sparse-supervision geoscience problems, and it is the paper’s most transferable idea.

  2. The paper holds out whole dates rather than random pixels. It compares against a strong learned baseline (Trans-XCO₂) under the same split and observation mask, and it includes a component ablation. The multi-directional Mamba backbone alone already beats Trans-XCO₂ (held-out MSE 0.671 vs. 0.699). A global daily 0.05° land-and-ocean product is useful to the carbon-monitoring community.

Critical weaknesses
  1. The experiments do not isolate the central claim that LLM-elicited knowledge improves reconstruction. The priors are a deterministic lookup of climate zone, vegetation type, emission level and season. These attributes appear to be used only to build the priors; they are not listed among the backbone predictors in Sec. 3. So the “without knowledge branch” variant loses three things at once: (i) the LLM values, (ii) the categorical land-cover and climate information itself, and (iii) the adapter’s parameters. The 0.671 → 0.658 MSE gap (about 2% in MSE, about 1% in RMSE) could come from any of the three. Part of the “knowledge” also re-encodes existing inputs. The emission-level prior is a binned function of emissions already supplied through ODIAC, and the seasonal vegetation modulation overlaps NDVI/EVI.

  2. There are no variance estimates. All results appear to come from single runs. The ablation spread (0.658 / 0.664 / 0.666 / 0.671) is small. The convergence result is also small. Seed-to-seed variation could plausibly account for these differences. Epoch counts also do not measure wall-clock cost.

  3. The TCCON validation has no baselines. Table 3 reports only GeoPrior-Mamba, so it cannot show any improvement over CAMS, Trans-XCO₂ or the knowledge-free model. Over a three-year window, site-level R² is dominated by the secular trend and the seasonal cycle, both of which CAMS already captures . It is unclear whether the comparison is restricted to held-out dates. OCO-2 Level-2 bias correction is calibrated partly against TCCON, so TCCON is not fully independent of the training target.

Questions for authors

Does the knowledge-free variant receive climate zone, vegetation type, emission level or the seasonal factor in any form? Please add (i) the same adapter with learnable embeddings of these categories and no LLM values, and (ii) the full model with permuted prior tables. If the LLM priors do not beat (i), the main claim does not hold. If they do, the paper becomes considerably stronger. Please report mean ± std over at least 3 seeds for the main rows and ablations in Table 1, and for the convergence comparison in Fig. 3
What fraction of dates is held out, and how were they chosen (random days or contiguous blocks)? Are the validation dates used for Fig. 3 and model selection disjoint from the test dates? Does Table 2 / Fig. 2 include training dates? If so, please replace the 0.77 ppm entry in Table S2 with held-out numbers. With interleaved random days, slowly varying CAMS bias is shared with neighbouring training days, so a blocked split (e.g., holding out whole months or seasons) would be a stronger test. Was Trans-XCO₂ retrained on your split with comparable tuning? All predictors are on the 0.25° grid, so what information drives sub-0.25° structure in the 0.05° output? On held-out 0.05° cells, how does the 0.05° output compare with the 0.25° prediction bilinearly upsampled?

2 comments

Q1. Knowledge-free inputs and matched prior control

The knowledge-free variant does not receive climate-zone ID, vegetation-type ID, emission-level ID, or seasonal prior factors as separate inputs. It retains all common continuous predictors, including ODIAC emissions and MODIS vegetation variables such as NDVI/EVI. The branch-removal ablation therefore measures the joint contribution of the structured prior fields and the knowledge adapter. Removing this pathway increased held-out test MSE from 0.658 to 0.671 ppm².

To isolate the LLM-derived coefficient values, we added a matched randomly initialized learnable-table control. It retained the same categorical indices, table structure, adapter, backbone, and training configuration, while replacing the fixed LLM-derived values with 309 learnable coefficients. Across training seeds, the fixed DeepSeek-derived prior achieved a mean best-validation MSE of 0.6284, compared with 0.6380 for the learnable-table control, a relative reduction of approximately 1.5%. This suggests that the elicited coefficient values contribute beyond the categorical lookup structure and adapter capacity. We will report the corresponding standard deviations and complete seed list.

Figure 3 shows representative optimization trajectories. We do not interpret differences in optimization epochs as demonstrated reductions in wall-clock computational cost.

Q2. Split protocol, held-out evaluation, Trans-XCO₂, and 0.05° output

Date split. After excluding the earliest two dates required for the historical input, the remaining 1,094 dates from 2018–2020 were shuffled using split seed 42 and divided into 765 training, 164 validation, and 165 test dates. All observations from a date belong exclusively to one subset, and the validation and test dates are disjoint. Because the subsets are temporally interleaved, this protocol evaluates unseen dates within 2018–2020 rather than future-year generalization. A chronologically blocked evaluation has not been completed, and we do not claim persistence under stronger temporal distribution shift.

Full-period versus held-out results. Figure 2 and Table 2 summarize the complete 2018–2020 period and include training dates. Their RMSE of 0.77 ppm is a descriptive full-period result rather than a held-out estimate. It will no longer be used as held-out performance in Table S2; held-out comparisons will use the Table 1 test RMSE of 0.811 ppm.

Trans-XCO₂. We retrained Trans-XCO₂ using the same dataset, date split, and held-out OCO-2 mask. It achieved a test RMSE of 0.836 ppm, compared with 0.811 ppm for GeoPrior-Mamba. We will report the training settings, parameter counts, hardware, optimization epochs, wall-clock time, and inference cost for both methods, while documenting their hyperparameters separately.

Interpretation of the 0.05° output. All environmental predictors enter at 0.25°. A coarse decoder produces the 0.25° reconstruction, while a fine decoder predicts the final 0.05° residual correction relative to CAMS. Thus, 0.05° denotes the output-grid spacing and sparse target-supervision scale, not independent native information below 0.25°. Removing the coarse branch increased test MSE from 0.658 to 0.664 ppm², demonstrating a contribution from multi-scale supervision but not proving that the direct 0.05° output outperforms an upsampled 0.25° output. We limit our resolution claim accordingly.

Additional concern: TCCON evaluation

Table 3 is intended as an external ground-based consistency assessment rather than a comparative benchmark. It cannot by itself establish improvement over CAMS, Trans-XCO₂, or the knowledge-free model. Until matched comparisons using identical stations, temporal windows, spatial matching, and quality-control rules are available, we will not use Table 3 as evidence of relative improvement.

We will replace “independent validation” with “external ground-based consistency evaluation,” acknowledging the effects of shared seasonal and long-term variability on site-level R2R^2 and the role of TCCON in the OCO-2 bias-correction framework.

Thanks for the response. The split details, the retrained Trans-XCO₂ numbers, and the narrower 0.05° and TCCON claims answer most of what I asked, and the learnable-table control is what I was asking for.

My main concern is still there, though. The control is reported as best-validation MSE (0.6284 vs 0.6380), but validation is also what you used to pick checkpoints, and there’s no std or number of seeds. With a gap of ~1.5% in MSE, I can’t tell whether that’s real without seeing the test-set spread across seeds. You also didn’t run the permuted-table control. Without it, I can’t tell if the LLM values actually matter or if any fixed table just regularizes better than a learnable one. The other gaps in Table 1 are also small, and they’re still single runs.

I’ll keep my score.

Reviewer_r29fOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper proposes GeoPrior-Mamba, a global XCO₂ reconstruction model that combines a multi-directional Mamba backbone with structured process priors generated offline from an LLM. The LLM is used to organize knowledge about vegetation uptake, respiration, and anthropogenic emissions into fixed numericalThe paper proposes GeoPrior-Mamba, a global XCO₂ reconstruction model that combines a multi-directional Mamba backbone with structured process priors generated offline from an LLM. The LLM is used to organize knowledge about vegetation uptake, respiration, and anthropogenic emissions into fixed numerical priors; it is not used during training or inference. priors; it is not used during training or inference. The method improves over CAMS and slightly outperforms Trans-XCO₂, while the prior branch provides a modest accuracy improvement and noticeably faster convergence

Critical strengths
  1. Rather than putting an LLM directly in the prediction loop, the authors convert its knowledge into deterministic structured priors and inject them adaptively into the model. This is a sensible way to use LLMs in a scientific ML setting while keeping inference deterministic.
  2. GeoPrior-Mamba achieves an RMSE of 0.811 ppm on the held-out test set versus 0.836 for Trans-XCO₂ and 1.565 for CAMS, and the TCCON comparison provides an independent validation source.
  3. Removing the knowledge branch consistently hurts performance, and the prior-enhanced model reaches a comparable validation error roughly 104 epochs earlier than the knowledge-free backbone.
Critical weaknesses
  1. Removing the prior increases test MSE only from 0.658 to 0.671 and decreases R² from 0.925 to 0.923. The authors themselves characterize this as a moderate improvement.
  2. A stronger experiment would compare the proposed priors against manually constructed expert priors, randomized/shuffled priors, simple categorical embeddings, or priors derived directly from existing datasets. Without these controls, it is difficult to separate the value of the LLM knowledge from the value of adding an extra structured feature branch.
  3. The main experiment uses a date-based split within 2018–2020, so it primarily tests unseen dates rather than substantial temporal or spatial distribution shift.
Questions for authors

q1. Can the authors compare the LLM-derived priors with meaningful controls, such as expert-designed priors, shuffled/random priors, constant priors, or learned embeddings using exactly the same adapter? q2. How robust are the priors to the choice of LLM, prompt wording, and elicitation randomness? If multiple LLMs or prompt variants produce similar priors and downstream performance, that would make the proposed methodology much more convincing and reproducible. q3. Does the improvement persist under stronger out-of-distribution evaluation, for example, future years, spatially held-out regions, different satellite sampling regimes, or other XCO₂ datasets?

1 comment

Q1. We added a matched learnable-table control that retained the same categorical indices, table structure, knowledge adapter, backbone, and training configuration, while replacing the fixed LLM-derived coefficients with 309 coefficients learned from random initialization. Across training seeds, the fixed DeepSeek-derived prior achieved a mean best-validation MSE of 0.6284, compared with 0.6380 for the learnable-table control, corresponding to a 1.5% relative reduction. This result suggests that the elicited coefficient values contribute beyond the categorical lookup structure and adapter capacity. Separate frozen shuffled, frozen random, constant, and literature-derived table controls are not included in the current results. We will report the corresponding standard deviations and complete seed list in the revised table.

Q2. We independently generated a second offline prior using OpenAI GPT-5 with the same category definitions, prompts, output schema, constraints, and five-sample median-aggregation procedure used for the DeepSeek-V4-Pro prior. Under the same downstream configuration, the GPT-5-derived prior achieved a mean best-validation MSE of approximately 0.630, compared with 0.6284 for the DeepSeek-derived prior. The two independently elicited priors therefore produced broadly similar downstream performance, although this comparison does not establish statistical equivalence or invariance to the choice of LLM. Sensitivity to prompt wording remains to be evaluated.

Q3. The current protocol uses a temporally interleaved date-wise split within 2018–2020. On the held-out dates, the prior-enhanced model achieved a test MSE of 0.658 ppm², compared with 0.671 ppm² for the knowledge-free backbone. This demonstrates a gain on unseen dates within the study period, but not forward-year or spatial out-of-distribution generalization. The TCCON analysis is an external ground-based consistency assessment over the same period and does not replace a future-year or spatially blocked evaluation. Whether the prior-related gain persists in future years, spatially held-out regions, other satellite sampling regimes, or other XCO₂ datasets remains to be evaluated. We will revise the manuscript to state this limitation explicitly.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.