Dear Laura,

could you please submit a revised manuscript taking into account the comments by the reviewers.

Best regards,
Christian

Dear Laura,

while both reviewers agree that the revised manuscript has been improved, there are still unclear parts of your manuscript. Please revise your manuscript according to their comments (see below). When resubmitting a revised manuscript please include a detailed point-to-point response and a manuscript PDF in which all changes are highlighted.

Best Regards,
Christian

Reviewer #1
The major comments from my previous review were about the data used, the assumption of a
constant feedback parameter and the length/prose of the paper. While the authors have tried to
address all, I am not yet satisfied with the solutions and I recommend another round of major
revisions. I still believe the manuscript will become a valuable piece is the discussion of climate
sensitivity, as it provides a comprehensive overview of modes of internal variability.
Major comments:
1.The authors still use HadCRUT4 as if it were a global average. They justified this by citing
other papers that have done the same. The Nicholls paper seems to make the same mistake
as the authors. However, the other paper does not. Liang et al. (2020) use HadCRUT4, but
they do take into account that it is not a global average and that there is missing data,
especially around the poles. They use a mask of the CMIP output so that the spatial
coverage of the datasets is the same. This takes some work to implement, so I suggest the
authors choose any of the four datasets with global coverage. Instead of comparing
HadCRUT4 with CW14 (f.i. in Table 1, Figure 12), the authors can compare CW14 with
NOAAGlobalTemp v5. Dropping HadCRUT4 from the manuscript completely also helps
making the paper shorter.
2.3.HadCRUT4 uses HadSST3 for sea surface temperatures, which further shows slower warming
due to biases in ship measurements in comparison with HadSST4. As I understand it, even
the incomplete (not infilled) provisional version of HadCRUT5 shows more warming than
HadCRUT4. CW14 uses HadSST3 as well, potentially explaining why it warms more slowly
compared to some other global averages.
The authors have developed an application of EM-GC with blended observations, but
temperature output of CMIP6 to test whether EM-GC has predictive power for future
temperatures. This is not quite what I intended with my comment, but I admit I wasn’t clear
before. I had hoped the authors would develop a pure model-based test of predictive
power. The outcome of the blended result shows that EM-CG often underestimates ECS, but
the authors claim in the body of the text that it is a very good predictor.
The authors now examine a time-varying feedback parameter, which varies with radiative
forcing. They do not give justification for why they integrate a time-varying feedback like
that. Global feedback is thought to change because of cloud feedbacks above a slow-
changing ocean. A delay of a couple of decades between radiative forcing and the change of
feedback is therefore expected. Disregarding the physics lead to a biased outcome, as the
model is trying to fit the rise in the feedbacks too early, and it is only natural that would fail.
Scaling with RF would mean that there is barely any feedback in the first half of the
twentieth century, which is also unphysical.
Different formulations for time-varying global feedback exist for simple models, such as
(Armour et al., 2013; Geoffroy et al., 2013; Goodwin, 2018). All of these formulations have in
common that the feedback only changes some time after radiative forcing, with different
lags. I think the Goodwin approach is most suitable for adjustment into EM-GC. Goodwin,
also using a data-driven model, shows that the upper range of climate sensitivity is
extremely sensitive to the time-scale.
I further believe that getting an optimal global constant by fitting, and then adjusting the
4.5.model to include time-varying feedbacks will tend to favour the former. Ideally, the fitting is
done simultaneously.
I don’t see how the authors determined the uncertainty around the carbon cycle. I cannot
find a mention of 10% of Friedlingstein (which concluded that emission-driven simulations
warm a tad more than concentration-driven simulations in CMIP5). Ten percent seems low,
but this is not my expertise.
The paper is still quite long. In the minor comments I will make another set of suggestions to
make the paper easier to understand. This will not be an exhaustive list. There are good
guides on the internet for writing concisely, that have helped me become a better writer.
For instance: https://writingcenter.gmu.edu/guides/writing-concisely.
The EM-GC model does not model the carbon cycle explicitly, and discussion of the carbon
cycle may also be an option to remove. I don’t see the value of showing all SSPs in f.i. Figure
9. Consider dropping those with few CMIP6 models.
Geoffroy, O., Saint-Martin, D., Bellon, G., Voldoire, A., Olivié, D. J. L., & Tytéca, S. (2013).
Transient climate response in a two-layer energy-balance model. Part II: Representation of the
efficacy of deep-ocean heat uptake and validation for CMIP5 AOGCMs. Journal of Climate, 26(6),
1859–1876. https://doi.org/10.1175/JCLI-D-12-00196.1
Goodwin, P. (2018). On the Time Evolution of Climate Sensitivity and Future Warming. Earth’s
Future, 6(9), 1336–1348. https://doi.org/10.1029/2018EF000889
Armour, K. C., Bitz, C. M., & Roe, G. H. (2013). Time-Varying Climate Sensitivity from Regional
Feedbacks. Journal of Climate, 26(13), 4518–4534. https://doi.org/10.1175/JCLI-D-12-00544.1
Minor comments:
79: Replace ‘to designate future’ with ‘for the’: future and scenarios are redundant
101: ‘land-use change’: check hyphens throughout the entire paper
131: remove ‘of climate’
132: remove ‘because’, start new sentence at ‘this’
142: consider removing ‘Bony et al.’ sentence, I don’t see the use
150: due to this update, our model is
186: which update
202-205: long sentence
209: ‘that is our primary data source’, maybe replace with: ‘which we use as default’
220: rung→panel
235-237: unnecessary sentence
240: reword: for this simulation, kappa =1.28, W/m^2/C fits the OHC data best
242: remove ‘the’ before ‘IOD’
243: remove ‘temporal variations in’
245: slight -> small
343: remove ‘consequently’
347: remove ‘multiplicative’: factor is by definition multiplicative
348: split sentence after ‘2015’
354: remove ‘thus’
367: remove sentence, already clear
379: remove ‘scientific’: what else?
408: consider replacing ‘upon’ with ‘on’ throughout: make it easy for your reviewers and readers to
read your text
419: consider using the improved HadSST4, which removes biases in the ship measurements.
420: remove ‘variations in the strength’?
421: I’m not sure whether it’s appropriate to detrend using RF. Temperature lags RF quite a bit,
especially in oceans.
433: remove everything between brackets
435: surely the numbers are altered. I cannot imagine that the feedback parameter isn’t dependant
on AMOC in the fit.
438: consider using ‘use’ throughout instead of ‘utilising’
453: is this old factor still valid?
455: remove sentence ‘since ... whole atmosphere’, redundant.
459: remove ‘temporal’
481: remove ‘however’
505: equal to→of
510: upon consideration of→by including
534: colouring seems to be off in figure S10
539: remove ‘the computation of’
552: remove sentence, redundant
Section 3.1: move methodology to methodology section 2.2.1 (the bit about blending)
Figure 8: what interval is plotted for each study?
772: changed word order, it seems like we’re coupling a two-box model to 2.6
793: Cox et al. based on CMIP5
834: remove ‘indicated on each plot’, redundant
834-835: remove sentence, the reader will know how to do a global average
858: I don’t think bimodality is clear here. There seems to be outliers, but not two roughly equal-
sized groups of models. With so few models, passing any statistical test on bimodality would be
tough. Drop it?
863: remove ‘apparent in figure 9’, redundant
918: remove ‘our’, redundant
Figure 12: choose bigger bin size: CMIP models displayed weirdly
934: three significant digits not justified, two better
Table 1: same
991-1003: you seem to be repeating the table, making the prose difficult to read, condense to half
the size?
1015: since -> from / from ... onwards
1023: I don’t think either of them studied the entire climate system. Instead, those studies were
about the atmosphere.


Reviewer #2
After a careful reading of the manuscript, I found the authors have addressed most of my comments and questions, and the revised manuscript has been improved. However, there is still one issue that deserves more attention. In the previous review, I asked about the comparison of the AAWRs that are obtained from EM-GC and CMIP6 models. My concern was whether the AAWR from the EM-GC and the AAWR from the CMIP6 can be compared fairly, as the AAWRs were calculated by different methods (For EM-GC, using Eq. (9); For CMIP6 models, using REG method). The authors have revised this part, but if I understand correctly, they compared the AAWR from REG method with the AAWR from LIN method. There is no direct comparison between the REG method and the method used in EM-GC. The confidence in using REG method comes from the "close agreement of AAWR" found using both the REG and the LIN methods, which I find not very convincing. I would suggest that, if possible, the authors may apply the REG method to the EM-GC simulations (Note, do not use the coefficient C1 from Eq. (2). Use the new coefficient obtained from the REG method). Then, compare the AAWR from the REG method and the AAWR calculated from Eq. (9).

Dear Laura,

could you please address the points raised by the reviewer, especially Major Comment 3.
Could you please make explicit that your study estimates the effective climate sensitivity and not equilibrium unless you want to estimate ECS. If you make clear throughout the manuscript that you estimate effective climate sensitivity then you can disregard Major Comment 2.

The reviewer comment's are below.

When you submit a revised manuscript please include a point-to-point response and highlight all changes in the manuscript.

Best regards,
Christian




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.

[Back to Top]

Dear Laura,

thank you for submitting a revised manuscript. I am happy to accept this version. Congratulations.

Best,
Christian