I cannot support the acceptance of this paper at its present form due to the following major concerns:

1) The method and interpretation are very similar (nearly identical) to a recent publication (Xu et al., Nature, s41586-023-06398-6, 2023). There are essentially no new developments after I examined the whole paper, except for the slightly extended time coverage (by including three additional years). If the authors intended to revise the manuscript, they should extensively discuss how and why their method and results are different from the Xu et al. study. 

2) There appears to be very limited discussion about uncertainties in the derived datasets. The Zenodo archive only presents absolute concentrations, while no information about the expected error was included in the data or discussed in the paper. Especially considering that the paper presented strong dependence of the fire-induced PM2.5 on the specific fire inventory, what uncertainty envelope do you recommend in each of the dataset? After all, these datasets are expected to be used by the community for various applications, and such information is vital.

3) The paper only provided evaluation of the total PM2.5 using ground-based measurements, which is insufficient and partially reflected by the fact that the GFED- and QFED-derived products both agree well in terms of total PM2.5 while fire-PM2.5 are different systematically. Many recent products of fire-PM2.5 have been developed in North America (e.g., 10.1021/acs.est.2c02934, 10.1038/s41586-023-06522-6). The manuscript should use these critical data sources to inter-compare with the modeled fire fraction and the final estimates of fire-PM2.5.

Other comments:

1) I downloaded one example data, and found that negative values occur in occasional pixels. What are the physical meanings of them?  

2) Line 44, fire PM2.5 aerosols can be larger in size than urban PM2.5, see e.g., https://acp.copernicus.org/articles/19/6561/2019/

3) Line 71-81: These uncertainties seem not narrowed in this new dataset compared to the previous studies? Even the Xu et al. 2023 study itself has indicated similar differences in the derived fire-PM2.5 using four inventories. So what new insights/constraints have this work provided?

4) Line 93-94: I do not think computational cost is a major obstacle of machine learning approach. 

5) Line 108-110: Is it necessary/critical to do this specifically for China? Many other regions also bear with incomplete time series.  If the ML method is very sensitive to the availability of data over 2000-2013 in China, how uncertain are your predictions for e.g., India before ~2010 when observation data is available? 

6) Line 117-118: Please provide references of the method to convert AQI to PM2.5.

7) Figure 1b: It appears that log-scale color scheme is needed.

8) Figure 3: It looks abnormal to me that the cross-validation R2 (Panel b) values are stronger than the direct R2 (Panel c) in many years? Also, please do not use "simulated" for ML-corrected PM2.5. Could use "estimated".

9) Figure 6: I do not understand the "green slashes". Why are they so regularly distributed? 

In this paper, Hu et al. documented an important effort of generating a global daily fire-sourced PM2.5 dataset from 2000-2023. This dataset is derived using the following steps: 1) They use GEOS-Chem to simulate global daily all-source PM2.5 and apply ML to de-bias the all-source PM2.5 against surface measurements; 2) they then apply the ratio between simulated fire PM2.5 and total PM2.5 at the grid level to estimate the fire-sourced PM2.5. I think this is an important effort, and the dataset generated will become a valuable asset to the academic communities across different disciplines. I am excited to see such a dataset being made publicly available to the community.

With that being said, I agree with the other reviewer that the paper should do a better job of discussing its difference from the Xu et al., 2023 Nature paper, in addition to the extended temporal period (which is an important update in my opinion). In addition to a transparent and detailed discussion of the differences and contributions, I imagine the project could benefit from several potential analyses to further differentiate this paper from their prior contributions: 1) discuss the recent trends from 2020-2023; 2) discuss the differences between the GFED and QFED-based dataset (which do not seem to be the focus of their prior work); 3) a better quantification and discussion of the uncertainty of their datasets.

Other comments:

• One recent study found that GFED emissions inventory had a large positive bias in the western US in 2020. This raises potential concerns about the author’s methodology of using model-based fire/total ratios to derive their fire-source PM2.5 estimates. I think the paper could benefit from a more detailed discussion of this assumption.

https://pubs.acs.org/doi/10.1021/acs.est.4c05922

• Related to the comment above, I think the paper could benefit from a comparison with the more refined regional fire smoke PM2.5 estimates. For example, the authors could compare their two estimates with data from Childs et al (which was recently updated to include 2021-2023) in North America.

https://www.stanfordecholab.com/wildfire_smoke

• The difference between GFED and QFED-based estimates is so large that I think it warrants a more in-depth discussion of the potential reasons. Could the authors draw on prior research that evaluates these emission inventories to discuss the potential reasons?

For example: https://doi.org/10.5194/acp-20-969-2020

• Generating these two datasets (GFED and QFED-based) is an interesting contribution that allows researchers to evaluate the potential uncertainty. However, downstream users often just want to use the best available dataset. What can the authors say in terms of which one they recommend more or less? Also, I think the Xu et al. Nature 2023 paper considered other emissions inventories in their sensitivity analyses, why did the authors decide to focus only on GFED and QFED in this work?