The authors have made substantial changes to the manuscript and it is much improved. It is a potentially very interesting study but as described below I still believe major revisions are necessary prior to publication. I am still concerned about the overall significance and interpretation of their results. The authors have partially addressed the problem of variability in their discussion and conclusions. However, as explained below I am not still convinced of the current results due to the comparatively weak statistical tests, the lack of long averaging times and the lack of a convincing dynamical argument. I have tried to include some specific recommendations.
For the paper to be valid the authors need to address the variability of the atmosphere up front, not as an afterthought in the discussion and conclusions. They need to establish beyond a reasonable doubt that the simulation differences are due to changes in LULCC. The problem is not, as stated in the paper (p39, l 756-760) the short timescale of the LULCC circulation changes but that these changes are relatively small (Brovkin et al., 2013) and therefore can be difficult to distinguish from atmospheric noise. It is clearly encouraging that “that the time-sliced experiments with single-year forcing looped for multiple years, give results very similar to the transient simulations, pointing to the robustness of LULCC impacts” (L767-769), but this very general statement would need to be expanded on and quantified.
Thus, in order to recommend publication I would need to be reasonably convinced the difference between their simulations is actually due to LULCC. To show this they need to show: simulations with land-cover changes are (1) significantly different from those without land-cover changes and (2) that this difference is due to the land-cover change itself. Without establishing both (1) and (2) we cannot be sure that the circulation changes causing the ozone differences are not due to atmospheric noise.
Both Brovkin et al. (2013) and Lawrence et al. (2012) (referenced in the reviewed paper) examined the impact of land use changes on circulation. In each case they investigated the impacts of landuse from the difference between approximately 30-year runs. They both considered differences at the 95% level as significant. Brovkin et al. (2013) used multiple ensemble runs when available. The paper reviewed here uses the difference between 10-year averages and differences at the 90% level.
Thus the statistical tests to distinguish between the simulations used in this paper are really quite weak and apparently not consistent with literature. To establish that the differences between the simulations are real:
-the paper should look at the 95% level consistent with other literature;
-they should also keep in mind that when considering hundreds of gridpoints some will appear consistent regardless (see Wilks et al., 2016; Bulletin of the American Meteorological Society 2016 vol: 97 (12) pp: 2263-2273)
-the paper should not discuss non-significant results as meaningful (see below).
Even if the differences between the simulations are real atmospheric ‘noise ‘ can persist on the decadal timescale. Thus the authors need to address the fact the atmosphere can exhibit long timescale decadal changes which are due to low frequency variability, but not necessarily due to changes in LULCC. In other words the decadal simulations may be significantly different due to low frequency variability, but not due to changes in LULCC.
The simulations in Brovkin et al (2013) and Lawrence et al (2012) used 30-year averages (and in some cases ensemble simulations). This helps to distinguish the circulation differences in LULCC from atmospheric noise. The present paper used 10-year averages. One difference, however, is that the present paper uses fixed SSTs which might reduce the variability, but how much? I am not convinced 10 year averages are sufficient.
This is a problem the authors need to address in a substantive way.
1) The best solution would be to run additional ensemble simulations. I believe these could be the time-slice experiments. My guess is that when you look at the 95% level you will need to run additional simulations anyhow. It is possible, to save cost, you could run the simulations without the chemistry and just show the meteorological details are similar. It is not clear 55 year time-slice simulations are really necessary.
2) It is possible the authors could make the case that the transient and timeslice simulations are similar enough that we can be reasonably sure the simulation differences are due to LULCC. However, I think the authors do need to make this case quantitatively. Where are the simulations the same, and where are they different? Again their difference should be distinguished using the 95th percent probability level. The authors mention these type of simulations are similar but do not address this in a quantitative manner. Moreover, the timeslice experiments are 55 years long. Does it really take the model that much time to reach equilibrium? It seems the authors could more effectively use the timescale experiments to establish the significance of the differences by looking at different 10 year intervals, for example.
3) Hypothetically the authors could make dynamical arguments linking the changes in LULCC to the atmospheric changes. However, I am not convinced by the meteorological arguments in the paper. The meteorological differences between the simulations are of course self-consistent: the displacement of the jet-stream, the change in meridional temperature gradient, the changes in positions of anti-cyclones etc are consistent with each other, but this does not mean one can attributed these differences to LULCC. The albedo decreases seem to be related to the change in forest cover. However, neither of these seem very related to the changes in surface temperature or short-wave radiation. The northwards displacement of the jet occurs globally in two simulations with different land-cover changes and thus its relation to local changes in any one of the simulations is hard to discern. The authors make the point that the temperature increase occurs to the west of the region of LULCC but do not make a dynamic argument why this is so.
The authors should refrain from discussion non-significant signals. This is particularly the case when discussing the signal over Europe. From figure 7 the ozone changes are only significant over the ocean (at the 90th percentile level) and the temperature changes are not significant anywhere over Europe. Most of the changes discussed in this section are not significant at the 90th percentile. The discussion of changes in Europe should probably be dropped.
Minor Comments.
1. India. The precipitation increase appears to be displaced southward, not northward as stated in the text. I do not see evidence for an anticyclone in the figures, nor the consistency between the significant change in rainfall which seems to occur in the south of the domain and a displace cyclone.
2. Figure 1 is a nice figure, but in some ways is misleading. The thermal wind du/dz ~ dT/dy, and thus the jet is not related to dT/dy at a particular level as implied in Figure 1. Moreover, a displacement of the jet-stream does not lead necessarily lead to an anomalous high more than an anomalous low. It.is well established that changes in LULCC lead to upper level changes but the precise nature of these changes are probably quite complex.
3. The significance in the figures is still difficult to read. Some authors only color the parts of the diagrams that are significant, but there are other solutions.
4. L254: upper and mid-troposphere ozone observations?
5. L277: “emissions”: anthropogenic emissions?
6. Table 1: the last column “Other settings” is confusing as it is not clear what simulations this applies to.
7. L332: “integrated”: do you mean combined?
8. L439: “can be reduced”. This is not clear. |
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