|The authors have addressed two of my major comments almost to satisfaction (1 and 4), and for two others I'm willing to agree to disagree (5 and 6). However, the answers to major comment 3, and to lesser extent 2, remain unsatisfactory. |
Major comment 1)
I see no reason to include JMA in the analysis. It has an even lower spatial coverage than HadCRUT4, and is therefore not a global temperature. It's uncritical inclusion may therefore lead to a biased understanding of the topic. Furthermore, the images are really crammed. Similarly, Cowtan can be dropped, now that HadCRUT5 is out, improving Figures 6 and 7.
Major comment 3)
In Figure 14, the authors show that their model gives a good fit for a wide variety of assumptions on lambda. They show that an 50% higher ECS is very well in line with observations, and that even a doubling is still consistent with their criterion of X^2<2. Despite this, the authors say choosing a point estimate is reasonable, by visual inspectation of the graph (14e-h) that I find questionable and is not in line with the X2 < 2 criterion used in the rest of the manuscript.
With the insistence of using the assumption that lamdba is constant, the authors do not compute ECS and do not give a 'comprehensive analysis of uncertainties in AAWR, ECS, and projections of delta T in our EM-GC framework,', as they claim in the conclusion. Instead, the authors compute what is sometimes called effective climate sensitivity (https://iopscience.iop.org/article/10.1088/1748-9326/ab738f), and their analysis of future temperatures should be described as a lower bound consistently throughout the entire manuscipt. By comparing effective ECS with ECS computed with the Gregory method, they compare apples with pears. In discussing other papers, the authors also do not make this important distinction.
I had very much hoped the researchers would extend their model so that they compute true ECS instead. A simultaneous evaluation of time variation in lambda and aerosol uncertainty would lead to interesting results, considering the authors are able to account for internal variability.
* The authors state in the abstract that RF of aerosols is the main uncertainty, but show in their results that the time-component of lambda is equally uncertain (I quote: Increasing λ−1 by 50% results in a similar value of ΔT2100 as when utilizing a higher value of AER RF2011 (i.e. AER RF2011 less than −0.9 W m−2) in the EM-GC framework)
* The manuscript misrepresents the findings by Rugenstein. They did not study CMIP6 models (but mostly CMIP5, and some CMIP3), and they found that all models had an increasing feedback parameter over time, not just some
* Similarly, Marvel et al show that estimates from historical simulations strongly underestimate true ECS in virtually all CMIP5 models. This is misrepresented by saying 'some' models. The mean bias is 0.8 degrees. This difference would bring the manuscript in line with conventional estimates of ECS of around 3 degrees.
* In the authors want to include a reference for CMIP6, https://journals.ametsoc.org/view/journals/clim/33/18/jcliD191011.xml may work, shows that 26 out of 29 models show an increasing 1/lambda, also not 'some'.
* The manuscript misrepresents Goodwin et al (2018). That papers indicates that there are time lags up to a hundred years, and they model a time-scale lag of 20 to 45 years for the Cloud − spatial SST adjustment feedback. The manuscipt claims they have a maximum time delay of 20 years.
Major comment 2)
I had wanted the authors to compare model effective ECS with model Gregory ECS. This would show whether emperically-estimated effective ECS can be compared with model Gregory ECS. The authors have instead done a sensitivity analysis of what happens if less data is used. I don't think that exercise is insightful, and certainly does not answer my question.