|First, my thanks to the authors for the responses to my previous comments. While the manuscript has been improved, I feel some of the concerns I had with the initial submission have not been fully addressed. I recommend an additional round of revisions.|
My first point relates to Figures 2, 6, and 7. I appreciate the addition of Figure 2 and the added description for revised figures 6 & 7. The authors indicate that the median is being used to determine significance, yet the text still refers to the mean response in several places when drawing conclusions about the results
“The influence of aerosol is more clearly seen in regional mean precipitation that regional mean temperature (Figure 7a, b; Figure 2)…”
“Over Asia, the largest mean precipitation increase relative to 1980-2014 occurs in SSP1-1.9…”
“Over East Asia, JJA mean precipitation is not significantly larger in 1980-2014 in SSP3-7.0 until 2045-2054.”
Are the mean responses always the same as the median responses? If so, why not just say the median? If they differ, do they suggest conflicting conclusions? Additionally, regarding the statistical significance of differences, Figure 2 suggests the authors determine differences to be significant when the median of one scenario sits beyond the IQR of another scenario. What is done in the case where the median of scenario A is beyond the IQR of scenario B, but the median of scenario B is within the IQR of scenario A, are they considered significantly different? This happens numerous times in Figure 7. At other times, the responses in Figure 7 fail to meet the significance threshold of Figure 2, but the authors continue to describe the results as if they were significant. I have noted a few examples below.
“There is a clear aerosol-driven signal in future increases in global mean precipitation and hydrological sensitivity” I agree with the statement with respect to hydrologic sensitivity, but the precipitation anomalies are largely statistically indistinguishable from one another. For the NH-SH gradient, there is little indication until maybe 2045-2054, that the aerosols play a significant role there either (as determined using the method outlined in Figure 2) despite the authors claiming, “…anthropogenic aerosol is the main driver of trends in the interhemispheric temperature gradient until 2050…”
“Global aerosol reductions in SSP1-1.9 briefly cause faster warming over all Asian regions than the other scenarios considered, but this effect does not persist beyond the 2040s (Figure 7a).” Again, there is no statistically significant increase in temperature for SSP1-1.9 relative to the other pathways (except maybe relative to SSP3-7.0 over East Asia during 2025-2034). After continuing into the manuscript, the combination of Figures 5 and 8 seems to lend support for the argument of faster warming in SSP1-1.9, so maybe the manuscript.
The statements “The influence of aerosol is more clearly seen in regional mean precipitation than regional mean temperature,” and, “Over Asia, the largest mean precipitation increase relative to 1980-2014 occurs in SSP1-1.9 for 2025-2034 and 2035-2044,” both do not pass the significance test of Figure 2. Is this because they are referring to the mean instead of the median? Figure 11 does support the statements made in discussion of Fig 7, but there is no indication of significance or robustness in that figure. With the presence of outliers, it is hard to know whether the mean values are biased in Figure 11.
In short, perhaps a different test is needed to support the statements the authors are making. In the manuscript’s present form, the conclusions are consistent with the results, but are not supported by them with sufficient rigor. While the conclusions may ultimately be true, it is hard not to remain skeptical that the aerosol signal is “clear” or can be considered the “main driver” of the precipitation differences found in the simulations.
I also want to bring up the issue of land use land cover change (LULCC) again. The authors cite a paper (Singh et al. 2019b) that, along with additional references made within that paper, highlights the potential for LULCC to be just as important as other forcing agents on regional scales. The authors note this, but only show that globally LULCC is much smaller than aerosol and GHG forcing. The authors do bring up the regional impact LULCC may have in discussion of the South Asian results, but there is no discussion of LULCC with respect to the Asian or East Asian regions. Without calculating regional forcings, how are we supposed to know what the pattern of LULCC should look like among the different pathways. What if the LULCC forcings bring about the same pattern of responses in precipitation as do aerosols? While the model output may not allow for these calculations to be made reliably, it still merits additional discussion within the manuscript.
“Comparing the SSP2-4.5aer and SSP2-4.5 responses (Figure 12 vs. Figure 13 for MIROC6…) shows that aerosol largely acts to offset the GHG-driven response, rather than determining the overall pattern of the response.” How do we understand this by comparing these two figures? Many of the anomalies are the same sign as the eyeball-interpolated trend in the SSP2-4.5 figures… so why does that make the SSP2-4.5aer response an offsetting effect for GHGs? This dipole concern in Figures 12 and 13 leads into a bigger question about the dipole. Knowing that the responses over South Asia (Figure 7) are not in agreement with the aerosol driven paradigm of Figure 2, how should the dipole pattern be interpreted?