This paper analyzed changes in surface air temperature over China in response to stratospheric aerosol injection (SAI) geoengineering. The authors did so by analyzing existing G4 multi-model SAI simulations from the Geoengineering Model Intercomparsion project. The authors used the method of Kashimura et al. (2017) to decompose SAI-induced changes in shortwave radiation into components of solar reduction, albedo change, cloud cover change, and water vapor change. Using this method, the authors further examined spatial pattern of surface shortwave radiation change and its contributors over China.

This paper itself is straightforward and scientifically sound. However, it lacks scientific insight. I see little new scientific findings this paper offers. It essentially applies an existing method and uses existing multi-model dataset to a regional study. To put it in another way, if similar studies are done for another country/region, does it merit another publication?   

Speific comments:

Lines 31-32： Recent reports such as IPCC special reports on 1.5 degree warming treat CDR and SRM separately and no longer lump them together as geoengineering.

Lines 51-52: SAI does not necessarily reduce precipitation. It only reduces global mean precipitation if SAI is used to compensate GHG-induced global mean warming.

Lines 58-59: Possible ozone depletion due to SAI is not a result of SAI induced cooling.

Line 66: It is important to note that volcanic eruptions are just imperfect analog of SAI.

Lines 70-76: It is not clear what is the novelty of this study. The authors state that no previous studies have analyzed effect of SAI on surface air temperature over China. However, this is a very weak justification of the novelty of this study. What new scientific insight we can obtain from this study? In other words, if someone writes another paper, stating that no previous study has focused on surface air temperature response over another region/country, can it be justified for publication?

Lines 108-113:  Everything stated in this paragraph is self-evident.

Lines 114  Is it necessary to repeat the method and equations of Kashimura et al. (2017) in detail? What is new here?    

Line 222： Why surface cooling increases upward LW radiation?  

This is a carefully done and well written study.  I appreciate that the authors are able to use old simulations to do new science.  I have a few minor comments and one major one.

My major comment is similar to that of Reviewer #1 about the novelty.  I think there are good reasons to look at specific regions and try to understand them better.  Such investigations could warrant a new paper if they provide insight.  My problem is that the authors have not provided much insight that is specific to China.  The analyses they did could easily be applied anywhere in the world.  It would be much more useful to add some discussion about something specific to China that requires more in-depth analysis.  I won’t decide for the authors what they should focus on – there are lots of things to choose from.

I would appreciate a much more nuanced picture of geoengineering than you’re providing.  On lines 52-53, you talk about slowing of the hydrologic cycle.  That’s true, but climate change accelerates the hydrologic cycle, with some pretty bad consequences for a lot of people.  One lines 54-55, you talk about overcooling of the tropics and undercooling of the poles.  That is not a foregone conclusion – see Kravitz et al. 2016 (ESD) or 2017 (JGR).  On lines 55-57, you talk about termination.  That is a risk, but it’s less of a risk for lower magnitude deployments of geoengineering and a greater risk for higher magnitude deployments.  Your discussion of risks needs appropriate context.  Another example is line 62ff.  What you say is true, but it depends on the amount of geoengineering.  Irvine et al. (2019) found that with only a little bit of geoengineering, most regions would benefit under a wide variety of metrics.

Line 69:  China has been studied in several papers, but not explicitly or in much detail.  Also see my major comment above.

Line 175:  This is a strawman argument.  It wasn’t designed to return the temperature to climatological RCP4.5 levels.

Lines 200ff:  Instead of increased downward LH, it should be decreased upward LH.  The actual LH doesn’t become negative.

Lines 204ff:  Why does LW decrease?  (My guess is water vapor, which you talk about later in the paper.  But you should say so here.)

Line 212:  These changes are quite small.  Or did you mean these to be 10, 4, and 6%, respectively?  (Same comment for lines 224-225.)  In either case, are the changes statistically significant?

Line 221:  I don’t understand this explanation.  Cooling should reduce upward LW, not increase it.

I like Figure 11.  I’ve never seen something that clear before.

I recommend major revisions, due to the reasons below and the 16 comment on the attached annotated manuscript.

Fundamentally, this paper ignores an important component of climate change, and that is advection of energy.  Surface temperature does not just depend on vertical energy fluxes, but also on changes of atmospheric circulation.  By ignoring impacts on atmospheric circulation and wind patterns, as well as on storms and cloudiness, it ignores fundamental processes of climate change.

Why does this paper just look at China?  With all the data, why don’t the authors look at the entire globe?

What is the new science?  The results are what one would expect.  And there is little diagnosis of the reasons for the changes.

The authors only use three models, due to finding the data on ESGF, but the output from the rest of the models could have been obtained from the modeling groups.

I find the algebra and terms in section 2.3 confusing.  What is the difference between R and alpha?  They are both reflection.

There is a supplemental file, but it is not referenced at all in the manuscript.

It is great that they evaluate the models first before using them, but although the Taylor diagrams look pretty good, there are still substantial biases.

The manuscript is in quite a small font.  In the future, make it larger to make it easier for the reviewers.

Review of “Impact of stratospheric aerosol intervention geoengineering on surface air temperature in China: A surface energy budget perspective” by Zhaochen Liu and others

This paper investigates the effect of the solar radiation modification on the downwelling solar radiation at the surface over China and hence on the surface temperature. For this purpose, it uses the simulation data from the G4 experiment from 3 climate models of the Geoengineering Model Intercomparison Project (GeoMIP). In G4, SO₂ is injected into the stratosphere at a rate of 5 Tg SO₂ per year on the RCP4.5 emission scenario. The analysis in this paper focuses on the contribution of key processes involved in the reduction of solar radiation at the surface. Four processes are assessed: AOD changes in the atmosphere due SO₂ injections, water vapor changes due to tropospheric cooling, changes in clouds and surface albedo. A simple 1-layer atmosphere model is used to facilitate the understanding. This decomposition of changes in downwelling shortwave radiation at the surface by a simple model is an elegant approach that helps to understand the complex interaction between various physical processes in climate models. The presentation is fine but could be improved in the revision. The paper could be accepted for publication after the main and specific comments listed below are addressed.

Main comments:

Clear insight into the contribution of water vapor changes and albedo changes should be provided in the revision. A colder atmosphere holds less water vapor – 7% decrease in water vapor per deg C decrease in temperature. Reduced water vapor causes reduced absorption of solar radiation that is coming down. In the case of surface albedo, colder temperatures are likely to lead to an increase in snow on the surface which would reflect more sunlight and hence a reduction in net surface shortwave radiation.

The authors find that there is decrease in clouds over China in the G4 experiment (Figures 7, S1 and S2). This decrease allows more net solar radiation at the surface. Some insight into the reason for the decrease in cloudiness in G4 should be provided in the revision.

Equations 8-11: How are these equations implemented in this work to estimate the 4 contributions discussed in section 4.3? This should be briefly discussed right after the derivation of these 4 equations. Also, the connection between these 4 equations and discussion in section 4.3 should be discussed in the beginning of section 4.3

Why does this focus on China? Why not the entire global domain? The rationale for the choice of the domain should be discussed in the revision.

Specific comments:

• Line 45: delete “simulating”
• Line 50: change “the decreasing” to “decrease”.
• Lines 53-55: the overcooling of the tropics and undercooling of the polar regions would happen only if SRM is designed to offset the entire global mean surface temperature change. This important point should be included in the discussion here.
• Lines 55-59: SRM does not address the ocean acidification problem caused by increasing levels of CO₂ in the atmosphere. This deficiency of SRM should be also mentioned here.
• Line 70: Why do the author assess only surface temperature change? Why not the other important climate variables such as precipitation?
• Line 79: change “the simulations in the G4 experiment” to “the G4 experiment”?
• Line 79: provide a reference for the first phase of GeoMIP.
• Lines 108-118: What is the rationale for using the 1-layer atmosphere model in this study? What are its advantages and disadvantages? This should be briefly discussed.
• Line 122: For clarity, change “R is the fraction of reflection” to “R is the fraction of solar radiation reflected by the atmosphere”
• Line 155: “All the SCC are significant at the 99% level” How is this assessment made? Taylor diagram does not provide an assessment of the significance level of the correlation efficient. The method used for the statistical assessment should be briefly discussed.
• Line 180: the lack of differences in trends between G4 and RCP4.5 is expected because the magnitude of the radiative forcing is the same in the experiment except in the beginning when aerosols are suddenly injected in the G4 experiment.
• Line 205-208: The sign convention of LW is not clear in this paper. Is upward or downward LW is considered positive? This should be clarified in the revision.
• Lines 211-212: The figures show a decrease in clouds, but the text says clouds increase. The authors should carefully check their analysis.
• Lines 215-216: The link between the deficit of downward LH and flux and increase in cloud cover is not clear. Either delete this discussion or provide clarity.
• Line 220-223: The discussion is unclear. Revise the text
• Lines 251-253: The message from this sentence is not clear. Revise the text for clarity.
• Line 303: The Tilmes et al. 2018 paper discusses injection at multiple locations and not regional injections.
• Figure 1: I believe cs and cl are interchanged in the illustration. Should be corrected.
• Figure 2: The last line of the caption: The oblique dotted line cannot be seen in the figure. Revise the figure or the caption.