Both reviewers raised major concerns with this manuscript, which I don’t think have been sufficiently addressed in either the response or the revisions. I share the reviewers’ concerns about the experiment design used in this study, and would like to see these addressed in more detail before returning the manuscript to the reviewers.

The observed precipitation trend is evaluated based on only 10 years of data, and there is no discussion of how this trend compares to either longer term trends, or internal variability. The trend is also based on only one observational dataset.
• I think it is important that we see a comparison between the GPM data and other precipitation datasets such as GPCP to give a sense of how robust this observed trend is.
• It is also important that the authors show a longer precipitation timeseries, and evaluate the interannual variability, to give some context to the magnitude and significance of the trend. Reviewer 2 is concerned that 2010 and 2011 were anomalously wet, and thus bias the trend. They have plotted data from 2000 – I ask the authors to at least do the same, and would strongly encourage them to plot an even longer timeseries to provide more context. It is stated in the abstract that Australia experienced anomalously dry and warm conditions since the 2010s, but, beyond a few citations, there isn’t any evidence in the manuscript to support this.
• In the response document, the authors state that the observed trend is calculated from 2010-2019 instead of 2013-2019 to minimize the internal variability. This is still a very short time period, and a quantitative assessment of internal variability is required if readers are to be confident that it is a forced trend.

The reviewers also raise important concerns about the experiment design, which warrant more discussion than they have been given in the current response and revision. I am not convinced by the response to reviewer 2, and think the authors undermine their own interpretation of their results in this response. Equilibrium runs are an excellent tool for understanding the physical response to forcing, and for identifying the mechanisms for particular responses, as the authors have done in this study. However, care needs to be taken when comparing them to real-world changes. As the authors state in their response, ‘the relatively short period from 2013 to the present may not provide enough time for the climate system to fully respond to aerosol changes’. But, this full response is exactly what their equilibrium simulations show. So, how can these experiments be used to quantify an aerosol contribution to an observed trend, as the authors do in their manuscript? Is it possible to use such simulations to make anything more than qualitative statements about observed trends? One could perhaps quantify the Chinese aerosol contribution to a modelled response, but this would require other forcings to be considered. Reviewer 2 is recommending rejection of the manuscript based on the experiment design. I would like to see a more detailed discussion of the design of the study, and the implications of comparing several hundred years of simulated equilibrium responses to just 10 years of observed data, in both the response to the reviewers and the revised manuscript before making a decision.

I am confused by the interpretation of the low bias in the PM2.5 and AOD trends in CESM1 found in the response and the revised manuscript. CESM1 is known to underestimate PM2.5. The authors have calculated a change in PM2.5 and found that it is small compared to the observed change. If this is based on an absolute change, and the background PM2.5 in the model is low, then one would also expect the change to be small compared to observations. However, even though aerosol concentrations and AOD in the model are low, CESM1 has a relatively large aerosol forcing. Thus, a small absolute change in PM2.5 or AOD may result in a large forcing in the model. I don’t think a small absolute change in the model necessarily implies an underestimate of the forced response. How do the percentage changes in PM2.5 and AOD in the model compare to the percentage changes in observations, for example?

Thinking back to the discussion of precipitation, it would also be good to know more about the significance of the observed trend. The emission reductions have been very large, but how significant is the change in AOD? Is there potentially a contribution from internal variability here that accounts for some of the model underestimate of the change relative to observations?

In addition to addressing the major comments above:
• it is necessary to improve the indication of significance on the map figures in the manuscript. The shading is difficult to see in many of the figures, both on my screen and on a printout.
• I would like to see some discussion of how these results compare to previous studies assessing the Australian precipitation response to Asian aerosols. Rotstayn et al. (2007) and Fahrenbach et al. (2023) are cited in the introduction, but are absent from the results and discussion sections.

There is a nice experiment, and some nice analysis of it in this paper, but there are still major concerns about the framing of the work and the interpretation of the results, and we cannot proceed to publication until these are resolved. It might be that they cannot be resolved. In which case, the authors should motivate their study based on the large emission changes, rather than the observed precipitation, and frame it as a speculative study of the potential responses. However, the issues with interpretation raised by all reviewers must be addressed regardless.

Framing
The premise of the paper is that Australia has experienced anomalously dry and warm conditions since the 2010. The authors then hypothesise that aerosol reductions in China since 2013 have contributed to this.

The observed precipitation trend is based on only 10 years of data, and there is still no discussion of how this trend compares to internal variability. The additional Figure S12, provided in response to my comments, raises more concerns here than it solves. The abstract claims that the period since 2010 was warm and dry in Australia, but the mean of the two periods highlighted in Figure S12 are almost identical. There is no evidence in that figure that Australia was anomalously dry since 2010.

Figure S14, provided in response to my comments, is reassuring, as it shows that multiple datasets agree that there has been a drying since 2010. However, I disagree with the authors’ conclusion that Figure S12 ‘clearly shows an increasing precipitation trend during 2001-2010, followed by a decreasing trend during 2010-2019.’ What I see here is variability. To be convinced that the trend since 2010 is anomalous, it needs to be compared to all other 10-year trends in ERA5 (using the available data from 1940 to the present to evaluate this). Is the negative trend from 2010-2019 unusually large in the context of 1940-2019?

Figure S12 also highlights the dependence of the 2010-2019 trend on what appears to be anomalously high precipitation in 2010 and 2011. Without these years, the trend would be markedly reduced. This is important, and more so in this case, since the driver that is being explored in the study occurs over 2013-2019. The authors should address the concerns from Reviewer 1 about the sensitivity of the trend to these years, particularly in light of Figure S12.

Analysis
The authors perform an equilibrium experiment to examine the Australian response to emission changes in China, North America and Europe, and everywhere except China. This shows that the response to Chinese emission changes between 2013 and 2019 is larger than that to emission changes in other regions. It also shows that the pattern of the precipitation response to Chinese emission changes is different to the response to emission changes elsewhere. The authors also show a strong seasonal component to the response. They also discuss the mechanisms for the response.

Neither the reviewers nor I have substantial comments on the analysis at this stage, as the points raised in review have focussed on the framing and interpretation of the study.

Interpretation
The authors claim that the warming and drying seen in response to Chinese emission reductions in their equilibrium experiments accounts for some of the drying and warming seen in the real world.

Reviewer 1 is concerned about the use of an equilibrium experiment to interpret real-world changes that have happened over a 7-year period. They point to literature that shows that the fast response of Australian precipitation to Asian aerosols can have the opposite sign response to the slow response, and therefore caution that an equilibrium experiment cannot be used to interpret the drivers of a fast change in the real world. It is important that the authors address these concerns.

There are also some inconsistencies and errors in the response to my comments on the interpretation of the experiment. The authors correctly note that ‘the relatively short period from 2013 to the present may not provide enough time for the climate system to fully respond to aerosol changes’. There then needs to be some discussion of the differences between the fast and the slow responses to aerosol changes. As the climate system may not have had time to fully respond to the aerosol changes, how do we expect an equilibrium simulation (where this has happened) to compare to the real world (where it may not have happened)? Can the authors demonstrate that the equilibrium response can be reached within the observational period, so that we can use this experiment to interpret real-world changes? If not, can they comment in detail on where they might expect their experiment to differ from the real-world response? The perturbation is applied as a step change in the equilibrium experiment, so it should be possible to find the time taken for the system to reach equilibrium in this case, and to assess whether the short-term response differs to the equilibrium response. Reviewer 1 also suggests an additional experiment to examine the fast response explicitly. This is a relatively cheap simulation compared to the equilibrium runs, and would only need to be performed for the China experiment.

The authors have removed most direct attribution statements from the text, but Reviewer 2 highlights one that remains, and should also be removed.

Be careful not to include attribution statements in the abstract:
L33: Suggest ‘drier and warmer conditions in Australia’ in place of ‘Australia’s drier and warmer conditions’
L34: ‘trigger’ in place of ‘triggered’
L37: ‘results’ in place of ‘resulted’
L42: ‘cause’ in place of ‘caused’
L43: ‘potential impact’ in place of ‘impact’

L196: Where were SSTs and SIC prescribed from?
L287: Time -> time
L435: You have analysed the Asian regions separately. Do they indicate that Liu et al.’s responses to Asian aerosol changes might have been insignificant because of cancellation between the responses to aerosol changes in different parts of Asia?