I find the general idea of this study quite innovative. In particular, the use of crop-model simulations to generate training samples, combined with remote-sensing time-series data for high-resolution yield estimation, has clear methodological value. However, I believe several aspects of the manuscript need to be further strengthened to improve its rigor, interpretability, and the practical usability of the resulting data product.

1.Clarify the use of the term “Label-free”.

The manuscript currently presents “Label-free” as a central contribution, but this term may be somewhat misleading. I suggest that the authors define it more precisely, for example as “field-label-free training,” “simulation-driven training,” or “simulation-driven yield estimation.” This distinction should be clearly stated in the abstract, introduction, and methods sections to avoid the impression that the entire study is completely free of any field observations.

2.Add comparisons with existing yield products.

The manuscript would benefit from a more systematic comparison with existing public yield products, such as SPAM and the “A 10 m maize, rice and soybean yield dataset from 2016 to 2021 in Northeast China” dataset. Both visual comparisons and quantitative accuracy assessments would help demonstrate the added value of the proposed product. In addition, the reported accuracy appears to be lower than that of current existing machine-learning-based yield estimation studies. The authors should discuss the possible reasons for this difference, such as the simulation-to-reality gap, limited field observations, simplified management assumptions, or uncertainties in remote-sensing inputs.

3.Include additional model-structure comparisons.

To better justify this model choice, I suggest adding other time-series models, such as LSTM and Transformer-based models, as baseline comparisons. This would help show whether GRU is indeed the most suitable architecture for this task, rather than simply being one possible option.

4.Strengthen the mechanistic interpretability analysis.

The manuscript mainly relies on feature-combination experiments to assess the effects of different input variables. I think it is not sufficient to support a strong claim of “mechanistic interpretability” .I suggest incorporating model interpretation tools such as SHAP to quantify the dynamic contributions of different factors across growth stages to the final yield estimation. This would provide a clearer understanding of how the model uses information from different phenological periods and environmental variables.

5.Provide confidence or uncertainty layers for the yield product.

For a data product intended for practical use, a single yield estimate may not be enough. I suggest providing annual 10 m confidence or uncertainty maps in TIF format. Such layers would allow users to identify where the yield estimates are more reliable and where they should be interpreted with caution.

6.Report uncertainty in model-performance metrics.

Machine-learning models are affected by randomness in model training, sample splitting, and parameter initialization. Therefore, I suggest reporting uncertainty ranges or confidence intervals for the main accuracy metrics. Methods such as bootstrap resampling, repeated random splits, spatial cross-validation, or Monte Carlo experiments could be used to report the mean and 95% confidence interval of R², RMSE, MAE, and bias. This would make the performance assessment more robust and more convincing.

7.Explain how the model captured typhoon-related flood-induced yield losses in 2023.

The manuscript highlights the model’s ability to capture yield losses caused by typhoon-related flooding in 2023. However, if WOFOST was mainly run under a water-limited mode, the simulated training samples would primarily represent water deficit or drought stress rather than yield losses caused by excessive soil moisture or waterlogging. The authors should explain which input signals allowed the model to detect flood-related yield reductions. Was the decline in LAI the main pathway? Were precipitation anomalies, soil moisture conditions, abrupt vegetation-index changes, or post-disaster canopy recovery also involved? If waterlogging processes were not explicitly represented in the simulations, this limitation should be clearly acknowledged in the discussion.

8.Expand the range of WOFOST simulation scenarios.

Although the study generates a series of crop-model simulations, the simulation settings appear to be relatively simplified. For example, soil parameters are limited to four major loam types, and only four fixed sowing dates are considered. These assumptions may not fully capture the diversity of real-world field conditions. The authors should consider adding more combinations of sowing dates, soil parameters, water management, fertilization levels, and irrigation scenarios to improve the representativeness of the simulated training samples.

9.Add validation at a finer administrative scale.

Validation based only on prefecture- or city-level yield statistics may be too coarse and could mask local spatial biases. I suggest collecting county-level maize yield statistics for the three northeastern provinces from 2019 to 2024, if available, and using them for additional validation. This would provide a more rigorous assessment of the spatial accuracy of the proposed yield product.

10.Discuss the simulation-to-reality gap more explicitly.

A key assumption of this study is that a deep-learning model trained on crop-model simulations can be successfully transferred to real remote-sensing conditions. Therefore, the gap between simulated samples and real-world fields is central to the reliability of the method. I suggest adding a dedicated discussion of this simulation-to-reality gap, including uncertainties related to crop-model parameters, management practices, remote-sensing LAI retrieval, meteorological inputs, and the absence or simplification of certain real-world stress processes such as flooding.