|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.
Review of Tarin-Carrasco et al., Reducing future air pollution-related premature mortality over Europe by mitigating emissions: assessing an 80% renewable energies scenario. Submitted to ACPD.
General: Tarin-Carrasco et al. use WRF-Chem to study emissions scenarios and subsequent impacts on human-health throughout Europe. Included in their analysis are “present” conditions, a future climate forcing scenario, and a renewable energy adoption scenario. Within each scenario, the effect of projected changes to the population’s age distribution are explored. The authors report that the current health burden attributable to PM exposure in Europe is high and will increase in the future (albeit with slight benefits following a stringent renewable energy strategy), almost exclusively driven by an aging population.
Overall, I believe this manuscript requires significant modification before it can be considered for publication in ACP. I outline my comments below and attempt to provide guidance, where possible.
-The REN80 scenario is framed as an “80% renewable energies scenario.” However, this scenario only considers emissions from the energy sector. Meanwhile, mobile, residential, and industrial emissions are left alone. This seems to be an important oversight since these other sectors have clear impacts on the trajectory of the energy sector. For example, vehicular electrification. If adoption of electric vehicles expands, as is expected, this will have a large effect on the energy sector. If residential heaters using wood combustion are replaced with electric heaters, that too would have a massive impact on primary PM emissions. It seems the title of the manuscript does not quite match the contents. Rather, the scenarios analyzed here are assessing what the PM impacts might be if the energy sector was 80% powered by renewables during the 1991-2010 period; not a future where Europe is 80% powered by renewables.
In addition, what’s notable to me is that we are today (i.e. 2021) closer to the “Future” time slice (only 10 years away from 2031) than the “Present” time slice (11 years away from 2010). With the benefit of hindsight in this situation, how is this 80% renewable energies scenario fairing? What is the 2020 contributions of renewables vs. nuclear vs oil vs coal vs gas vs other fuels? Is the REN80 scenario too optimistic? Seem about right? Too pessimistic?
-Why are the older RCP scenarios used and not the newer SSP scenarios? Why is the RCP 8.5 scenario used when it is such an unlikely scenario (Hausfather and Peters, 2020)? If one of the more “likely” scenarios were used, perhaps much of the reported climate penalty in the Iberian Peninsula would diminish. Also, please indicate in Table 3 which year of ACCMIP emissions were used for each case. I believe the FUT-P2010/50 simulations used present day emissions from ACCMIP, but it isn’t clear to me.
-Health impact assessments associated with air pollution exposure traditionally report results in terms of premature deaths. Premature deaths are a tangible number that is easy to understand (unlike YLLs and DALYs, in my opinion). However, issues can arise when attempting to communicate health burdens attributable to air pollution exposure. This is because changes in air pollution exposure is not the only variable affecting these health impact calculations. For example, this manuscript presents a scenario in which PM decreases throughout Europe, often in places > 1 ug/m3, except for some slight increases in the Iberian Peninsula and SW France (Fig. 4). However, calculated health impacts nearly double (895k to 1480k in Present and REN80-P2050 scenarios, respectively). Unless someone is familiar with the underlying concentration-response functions and how they are applied, this is likely very confusing. I believe the authors have an opportunity to (and should) update the presentation of their results in a way that can help the community more broadly communicate the health burden associated with air pollution exposure.
In Apte et al., 2018, the health burden associated with long-term PM exposure is reported in terms of decrements of life expectancy. What is advantageous of this health burden presentation is that the results are largely driven by differences in exposure. When health impacts associated with various scenarios (especially over long periods of time and into the future) are presented in terms of premature deaths, the results can be heavily skewed by changes in the size of the underlying population and age structure. When health impacts associated with various scenarios are normalized (e.g. # premature deaths per 100,000 habitants), the effects of changes to the population size are eliminated but the results can again be heavily skewed by changes in the age structure of the population. Table 4 illustrates both examples quite well. I believe health impacts reported in terms of decrements of life expectancy can mitigate the influence of non-air pollution exposure effects. I believe the Global Burden of Disease reports life expectancy per-country, which can help facilitate these calculations. Without such corrections, I believe many would generate misguided conclusions about the benefits of reduced air pollution exposure.
-The present-day health impact numbers reported here are noticeably high: 895,000 for Europe. For example, Burnett et al. 2018 report 647,000 premature deaths for Europe. Does the WRF-Chem set-up used here have a high PM bias? I’m curious, why not use “observed” PM from one of the various satellite products and apply the change in PM calculated from the CTM to one of those datasets? Essentially, use the CTM to calculate the sensitivity of each scenario and apply to “observations.”
-The differences in endpoint are discussed throughout the manuscript, including how the proportions change over time (e.g. much of Sections 3.5.1, 3.4, and Fig. 6). However, I believe the same baseline mortality rates (y0 in Eqn. 1) are used in both “present” and “future” simulations. It seems that these comparisons are difficult to make under those assumptions.
-Apte et al., Ambient PM2.5 Reduces Global and Regional Life Expectancy; ES&TL, 5, 9, 546-551, 2018.
-Hausfather and Peters, Emissions – the ‘business as usual’ story is misleading; Nature, 577, 618-620, 2020.