The authors seek to address the question of how much apparent temperature in Beijing will vary under different future scenarios of climate change (including geoengineering). This includes an analysis of whether different downscaling methods – either statistical or dynamical – yield different results. They find that, although both methods (when applied to results from 4 global ESMs) yield roughly similar results for the present day, the same is not true when inspecting the effects that climate change and geoengineering will have. The study highlights the important issue of changes in human-relevant variables such as apparent temperature (and the number of times a threshold is crossed) rather than relatively abstract variables such as global mean surface temperature.

I struggled with this review because I could not clearly identify the core contribution. The base idea of whether statistical downscaling or dynamical scaling results in different outcome estimates is certainly important, but this question has been thoroughly discussed in a companion paper by the authors which looks at the same data for the same domain from the same models, and was submitted recently to this journal (https://esd.copernicus.org/preprints/esd-2022-35). The remaining question is whether apparent temperature is differently affected than more conventional meteorological variables, which is a relatively boutique concern. The methods used to address this questions are nonetheless appropriate, and the data produced generally support the conclusions. However, the existence of the companion paper (which I recognize the authors do cite) makes the contribution of this manuscript incremental.

The use of multiple downscaling techniques with multiple models is interesting and well executed, and it is particularly encouraging to see applications to health-relevant outcomes. The biggest issue is a lack of significant impact, although I also have some methodological concerns. I have laid these out in detail below, starting with major comments. If the paper can be focused more heavily on outcomes – in particular, the effect that downscaling has on health-relevant impacts – then I believe it could significantly improve its relevance and impact. This would also help to address the issue that the paper is not particularly interdisciplinary, which is a stated requirement of ESD. As such, in its current state I cannot recommend it for publication.

Major comments

The greatest issue is the lack of a clear and impactful outcome. The methods applied are interesting in large part because they look at interesting scenarios (RCPs versus geoengineering versus recent past) and include a significant problem (the performance of statistical versus dynamical downscaling). However, these issues are the focus of a paper which is already under review, and as such cannot be the major novelty of a second manuscript. I therefore assume that the major conclusions regard the question of change in apparent temperature, with the authors finding that changes in apparent temperature will be greater under RCP 8.5 than under a geoengineering scenario, and that this is mostly because of increases in temperature. The issues I perceive here are twofold. Firstly, apparent temperature – while an important metric – is just one metric of impact, and a relatively straightforward one which is (evidently) mostly just reflecting changes in temperature. The manuscript would be greatly improved if multiple outcomes were assessed rather than just one, to see if the different downscaling methods have different impacts on such outcomes. This could include, for example, regional air pollution (if reported in any of the ESMs). Alternatively, a deeper analysis of the likely consequences – for example by attempting to quantify the differences in health outcomes or costs, and the degree to which different demographics or sub-populations are affected – would help to improve the interdisciplinarity of the manuscript. Secondly, the current analysis is somewhat limited, being mostly observational (report differences) rather than explanatory. The manuscript would be greatly improved if the authors could provide mechanistic explanations for their findings; why, for example, does WRF-based downscaling seem to result in such a different seasonality in AP – T compared to statistical downscaling?

My second concern regards the treatment of ERA5 data as an observational reference (L132-133). The paper would be significantly strengthened if the authors instead compared their simulations of the recent past with monitor data. Even if this monitor data is used in ERA5, showing that the simulations are capable of reproducing truly observational data rather than a reanalysis would provide more convincing evidence of model performance.

I also have a methodological concern regarding the method used to try and separate out the roles of different meteorological variables in changes in AP. It is not clear to me why a linear regression is used. The expression for AP is a simple (albeit non-linear) combination of variables, which can be easily and explicitly broken down to find how each one contributes to changes in AP. I suggest the authors at least evaluate how their contributions change if they calculate them based on the degree to which excluding a factor changes AP (i.e. contribution of T to AP is estimated by calculating change in AP with no change in T, but including other factors). The authors could also consider defining the derivatives of AP with respect to each factor, given that these should be well defined (and include the Clausius-Clapeyron relationship directly).

Finally, much of the analysis is rather subjective (e.g. lines 253-257 – “little difference”, “slightly worse”, “slightly better”). I would recommend that the authors revise the text to make use of quantitative statements, in particular from line 219 onwards. Furthermore, statements such as “There are no models with obvious regional differences” (line 287), “AP changes … are essentially the same” (line 296), “all ESM reproduce the ERA5 pdf well” (line 261), “striking differences” (line 318) and “ERA5… probably does not account for the broad overestimate” (line 234) lack rigor and are difficult to interpret or verify without some context (what counts as a broad overestimate, or an obvious difference? How big would a difference in the change in AP have to be to not count as essentially the same? Why?). A particularly significant example is on line 255, where it is stated that BNU-ESM’s performance is “slightly worse” than the other three models when using the ISIMIP method to inspect the recent past. This seems like a significant understatement; BNU-ESM’s performance appears to be significantly worse than the other three models (r ~0.85 compared to ~0.92 for the other three), predicting both too many extreme low temperatures and not enough moderately low temperatures (see Figure 4). This is central to the manuscript, since WRF appears to be able to “save” BNU-ESM, bringing its performance to at least be similar to that of HadGEM (albeit still worse than MIROC-ESM[-CHEM]).

Minor comments

L45-47: Need citations to support idea that apparent temperature is actually an important variable

Equation 3 is not exactly the Clausius-Clapeyron equation. It is an approximate form which fits some empirical data. Please provide the relevant citations for this relationship (most likely Tetens (1930), Murray (1967), and Monteith and Unsworth (2008)).

L162: Citation needed for US NWS

L164-166: The rationale for using NdAP_32 does not make sense to me. Since you are looking to identify an increase in the frequency of a rare event, why does the fact that it is rare mean that you should not use it? Similarly, why presume that the same outcome will apply for higher thresholds? I suggest revising the rationale

L168: “Since health impacts are more important where there are more people”: this seems like a value judgement, and not (I think) the intended meaning. I recommended simply stating that you calculated population-weighted changes.

The dark colors in Figure 6 make it nearly impossible to read the data.

Figure 7: please label the months.

Throughout: it would be helpful to see the baseline (undownscaled) results alongside the downscaled results, so that the readers might know how significant the differences between ISIMIP and WRF are compared to the differences between the original and downscaled outputs.

The purpose of this work was to compare the changes in apparent temperature across three future scenarios using two different downscaling techniques. The authors find that although both downscaling methods using ISIMIP and WRF reproduce historical observations, projections to future scenarios produce differing results. In general the authors conclude that changing temperature contributes most to changes in apparent temperature which is driven by a combination of 2-m temperature, relative humidity and windspeed to more accurately capture the physiological impact of a warming climate. They find that the occurrence of days exceeding a 32 deg C apparent temperature threshold across the Beijing-Tianjin megalopolis will increase in frequency under RCP 4.5 and RCP 8.5. They draw attention to GeoMIP scenario G4, designed to test SAI for its ability to mitigate risks from an RCP 4.5 scenario, finding that individual ESMs show no statistically significant differences in the number of days exceeding 32 deg C apparent temperature between G4 and RCP 4.5.

This paper is companion to a manuscript which focuses on the impacts of using different downscaling methods in the Beijing-Tianjin region. Therefore, my interpretation is that the core contribution of this paper is to quantify the effect of proposed SAI for this region, and to compare this effect across two downscaling methods. However, in some ways this comparison seemed like an afterthought, and the paper discussion centered on the differences in apparent temperature across the two downscaling methods. Therefore, I would agree with reviewer 1 in claiming that this paper is providing only an incremental contribution with this manuscript. If the authors were to reframe this piece to focus on key differences in SAI forcing vs the RCP 4.5 scenario using downscaling to identify sources of uncertainty in response, then I believe this would provide novel insight into SAI as a proposed technique.

Major Comments:

Use of the WRF and ISIMIP downscaling techniques across the four ESMs used was technically interesting and well executed. The use of apparent temperature was also useful, but given the results were largely driven merely by changes in 2 m surface temperature, it left the reader waiting for more of an understanding of the impact of the work.

1. To better frame this piece I believe the manuscript would be more clearly a departure from the companion piece if the framing of the paper was towards understanding the inter-scenario responses vs. the inter-method responses in apparent temperature. This would also make the work more appropriate for submission to the special issue on solar geoengineering. 
2. I would encourage the authors to include more than apparent temperature in these results. Given this is a monsoon region is there a reason why precipitation was not a variable included with apparent temperature? Soil moisture is also a useful metric when understanding SAI; and could give the reader more insight into expected agricultural outcomes.
3. The authors use AP>32 deg C as a metric citing that “similar differences between scenarios would apply for higher thresholds.” I would be curious for the author to provide us with results based on a 32 deg C threshold as well as a higher limit instead of speculating here. This could also help the author tie these findings to tangible impacts, such as mortality, or even economic outcomes.
4. I would encourage the author to more clearly tie the variable changes to tangible impacts; specifically mortality or economic outcomes. Or at least make this a larger portion of the discussion. The results of the two downscaling methods employed can then provide a measure of uncertainty in the expected response to SAI or future warming.

Stylistically I found much of the results section difficult to decipher and was confused by qualitative descriptions of changes and the use of subjective adverbs. This section should be reconsidered with some rigor to provide the reader with a clearer quantitative description of each piece of analysis. I was also unable to see any equations in this manuscript – and based on the comments of reviewer 1 I would second concern regarding the use of linear regression to quantify contribution of wind, RH and T to the apparent temperature.

Minor comments:

(88) : I was confused by “Beijing experienced an increasing trend of 12.7%  or 2.07 days per decade in extreme warm nights (Wangetal.,2013) …” does this mean they experienced a percent increase of 12.07% per decade in the number of extremely warm nights – I was unable to confirm this based on the citation provided.

I was also just a bit confused why nights was the most useful metric here. Has anyone done a study of the increase in warm days from 1978-2008. It seems in line with your paper it could be useful to provide information regarding the historical increase in surface temperature vs. apparent temperature in this region.  

(105) Define AP before using as an acronym

(109) Figure 1, Panels C and D color-bar labels should be added to specifiy units. I would also specific in the label what the red line is in figure 1, D – it seems that this is where the WRF domain terminates?

(127) Consider changing “climate forcing comes from 4 ESMs)” to something like climate simulations were performed by 4 ESMs – for clarity. As written it sounds like the radiative forcing from each model was extracted or somehow used separately.

(151-158) I am unable to see any equations in the pdf preprint view of this document (I presume this is not an author issue but rather a technical issue!)

(159-162) It would be useful to supply the read with values of the various thresholds for context as they read. I’m finding myself curious – what is the physiological maximum of the apparent temperature that humans can tolerate? What is the dangerous level? I would explain this before diving into your threshold value of 32 deg C to give the reader greater context. I would also provide citations of this empirically based scale.

Figure 2: I would ask the author to revise the labeling of the terms – I am not following the utility of the bar chart here. These terms should be telling the reader information about the contribution to AP from each of three terms, however the bar chart makes it seem like terms 1-3 should add to the given AP; but on close inspection they do not? Unless my pdf view is not showing me, the coefficients on each term are also not defined directly in the text.

Figure 3: I consider labeling the color bars of the bottom panels with # of days > 32 or something equivalent for clarity.

(234) : Missing “of” in the sentence “across most the North China..”

Figure 4: consider modifying the titles of the lower plots for clarity to also read ISMIP and WRF, since all four plots are showing AP.

Figure 5: The purpose of this figure is to compare the downscaling across WRF and ISIMIP – however the colorbar is constrained to give the reader cross scenario information. I would consider using different colorbars to for each scenario to better highlight differences in downscaling method, otherwise it seems these results cannot be well resolved by the reader.

Also, this figure is called back in line 285 as Fig. 5a-5c; please add alphabetic denomination in the figure paneling.

(320-331): in expressing results in this section be more direct in statements and consider breaking into smaller sentences. Be more quantitative in these expressions and consider modifying the descriptor “significantly” as it is unclear if this means humidity is changed at a statistically significant amount in this context. In several sentences in this section the author quantifies the contribution of humidity or wind to changes in AP – make more clear to the reader what this percent is referring to (e.g. amount to over 3% of the total change in delta AP in summer).

Figure 8: Consider changing stippling to a cross grid hatching to allow the reader to perceive values in the bottom WRF panel that are not statistically significant but still provide context to the reader.

(433) Change “warmer that 2m” to warmer than 2m