|The authors have addressed most of the comments raised by reviewers. However, there are still a couple of points that were not addressed and must be addressed before the publication. |
1. RCP8.5 scenario: The authors presented practical reasons for the RCP8.5 scenario (e.g., REPAIR initiative, simulation time), but did not provide the scientific justification of the use of RCP8.5. In their response, there was no discussion about the paper the reviewer had raised (Hausfather and Peters, 2020). They said it was discussed in the Conclusions section but it was not clear - why an unlikely scenario was chosen and why RCP8.5 was still feasible for this study.
2. Although both reviewers raised a question about the model simulation and further the use of incorporating "observed" PM, the revised manuscript still lacks a clear explanation. The authors provided two previous studies (Jerez et al., 2013; Ratola and Jimenez-Guerrero, 2016), but I think these are not appropriate references for the model used in this study.
Jerez et al. (2013) used a different chemistry model - CHIMERE, not WRF-Chem. Different chemistry models have a lot of differences in predicting PM2.5 concentrations (e.g., an order of magnitude differences in simulated organic aerosol concentrations: Figure 8 of AeroCom model intercomparison study by Tsigaridis et al., (2014)).
Ratola and Jimenez-Guerrero (2016) was also based on CHIMERE, not WRF-Chem. Furthermore, this study was only focusing on BaP, and BaP concentrations are on the order of pg/m3 (Figure 2), several orders of magnitude lower than PM2.5 (ug/m3).
If the authors do not evaluate their model, the authors should provide the previous studies with the "same" model configuration (or at least the same chemical mechanism and aerosol scheme if not the same model).
There was also no justification of using model results only, which was not constrained by satellite products or surface observations. I think there are many papers out there that used satellite products and/or surface PM2.5 observations to improve model results (Lee et al., 2015; van Donkelaar et al., 2016; Chem et al., 2020; McDuffie et al., 2021).
Lee, C.J., R.V. Martin, Henze D.K., Brauer M., Cohen A., and A. van Donkelaar, Response of global particulate-matter-related mortality to changes in local precursor emissions, Environ. Sci. Tech., 49(7), 4335–4344, doi:10.1021/acs.est.5b00873, 2015.
McDuffie, E. E., Martin, R. V., Spadaro, J. V., Burnett, R., Smith, S. J., O’Rourke, P., Hammer, M. S., van Donkelaar, A., Bindle, L., Shah, V., Jaeglé, L., Luo, G., Yu, F, Adeniran, J. A., Lin, J. and Brauer, M., Source sector and fuel contributions to ambient PM2.5 and attributable mortality across multiple spatial scales., Nat. Commun., doi:10.1038/s41467-021-23853-y, 2021.
Chen, H., Z. Zhang, A. van Donkelaar, L. Bai, R. V. Martin, E. Lavigne, J. Kwong, R. Burnett, Understanding the joint impacts of fine particulate matter concentration and composition on the incidence and mortality of cardiovascular disease: a component-adjusted approach. Environ. Sci. Technol. doi: 10.1021/acs.est.9b06861, 2020.
van Donkelaar, A., R.V Martin, M.Brauer, N. C. Hsu, R. A. Kahn, R. C Levy, A. Lyapustin, A. M. Sayer, and D. M Winker, Global Estimates of Fine Particulate Matter using a Combined Geophysical-Statistical Method with Information from Satellites, Models, and Monitors, Environ. Sci. Technol., doi: 10.1021/acs.est.5b05833, 2016.
3. Please provide the detailed methodology of model simulation. The paper nicely presented how to calculate premature mortality and emission scenarios in detail, but does not have a model description, especially for the aerosol scheme that is critical to PM2.5 estimation. I suggest the authors include these details but are not limited to: (1) Which aerosols were simulated, by aerosol type (2) Was it sectional, bulk, or modal? How was aerosol size less than 2.5 um calculated? (3) Was nitrate aerosol included explicitly in the simulation? (4) Was secondary organic aerosol simulated? if so, which SOA scheme was used? two-product, volatility basis set, or others? what kinds of VOCs were considered for SOA precursors? (5) Was thermodynamic partitioning of aerosols calculated like Jerez et al. (2013)? If so, was it ISORROPIA or MOSAIC or other? (6) Does aerosol affect cloud and precipitation in the model?
Minor comments are mostly clarifying questions.
4. The authors said they used climatological biomass burning emissions in response to the reviewer's comment. I fully agree with the authors' view about biomass burning emissions. It would be helpful if the authors could provide the absolute number of biomass burning emissions, especially for future studies that will compare their results to this study.
5. It looks like natural emission sources are different between PRE-P2010 and FUT-P2010, although anthropogenic emissions are fixed. If so, please provide the emission total of dust, sea salt, and biogenic VOCs for both present and future conditions.
6. "COPD, LC, LRI, and Other NCD barely change, since these causes are not too much sensitive to PM2.5 concentration as IHD (Figure 9), [...]": Figure 9 shows similar sensitivities to PM2.5 for LRI and IHD. It needs more discussion.