Using CMIP6 model simulations, the authors derive an emergent constraint that relates feedback from internal variability (IV) to forced feedback. They show that there are statistically significant relationships across models between components of IV feedback and forced feedback: a strong relationship for SW, a weaker relationship for LW, and an even weaker, but still significant and meaningful relationship for the net feedback. Using this relationship and combining it with observed internal variability, they show that more observations are needed in order to use this finding to actually constrain ECS. As an alternative to waiting for more satellite data, the authors extend the satellite record back in time by applying a correction model to reanalysis radiative fluxes, and thus constrain ECS to 2.5 K [90 % CI: 2.14 – 3.07 K], which is lower than current estimates from models, the IPCC, or Sherwood et al. 2020. Future satellite observations could be integrated into their method to update the estimates, and the authors quantify the quality of the constraint as a function of the number of observed years.

The paper is well-written, well-presented, clearly states its goal and provides evidence to support the claims, guiding the reader through the argumentation. The statistical methods are sound and used in an appropriate way. While I do have a long list of comments and questions, I want to stress that I enjoyed reading the paper and consider it a beneficial addition to the research on feedbacks and climate sensitivity. I have one main point to raise in criticism of this paper, which I will present in the following.

My main comment can be summarized as “What about the pattern effect?”

From the methods section, I understand that the feedback parameters are calculated as differential feedback parameters (referring to Rugenstein and Armour 2021, https://doi.org/10.1029/2021GL092983, please confirm if this interpretation is correct). All feedback parameters are estimated as the slope of N(T). For λ_ab, which time period is used for the regression? The full 150 years? We know that λ_ab changes considerably over time, both over the 150 years period (which is accounted for if the full 150 years are used for the regression), but also after this (e.g. Rugenstein et al. 2020, https://doi.org/10.1029/2019GL083898). According to that paper, ECS estimated from the 150-year span is an underestimate of the true ECS by 17 % in models. Would this affect the ECS estimate that the paper gives?

Further uncertainties may arise when leaving the model world. The historical simulations which are used to compute λ_it, are not capable of reproducing the observed SST patterns (e.g. Wills et al. 2022, https://doi.org/10.1029/2022GL100011). It is currently debated if the observed pattern of strong Western Pacific warming will continue or switch to stronger warming in the Eastern Pacific. This uncertainty implies enormous uncertainty for ECS (Alessi and Rugenstein 2023, https://doi.org/10.1029/2023GL105795). The point that I’m trying to make with these explanations is that it may very well be that the connection between λ_it and λ_ab is very different in the real world and models. While models produce El-Nino like patterns both in the present and future, the real world has warmed more La-Nina like until now, and we don’t know how it will continue. Since these patterns are tightly linked to λ_ab, the model results may not be applicable to the real world. This would be a major problem for the emergent constraint that the paper develops, because an implicit assumption of the emergent constraint approach is that the statistical relationship that is found in the models is applicable to reality.

I would like to ask the authors to discuss this uncertainty. In particular, do you think it affects the ECS range that is determined? If yes, how? If no, why not? If the authors agree that this could add substantial uncertainty, I propose mentioning this also in the last part of the abstract, which currently suggests that all uncertainties (except for the biogeochemical feedback) are accounted for in the 5 – 95 % CI.

In addition, I have other comments:

• l. 12, 21, 335 – 337: What biogeochemical processes does this refer to? Can you specify? I wonder if they are relevant for ECS, as the carbon-cycle does not matter for this concept of fixed CO2 concentration, and vegetation changes are not included in the definition of ECS

• l. 82 paragraph: As mentioned before, please state which years are used for the regression of λ_ab;

• l. 83 – 84: Is there a particular reason for subtracting the control state? I wonder, because a constant shouldn’t affect the slope estimate. It wouldn’t hurt the calculation, but I’m curious.

• l. 125: It is not immediately clear to me what was done here by “randomly permuting”. Were the R and T time series randomly matched (e.g. R from model 1 realization 1 and T from model 2 realization 1), and were the feedback parameters subsequently computed from these randomly matched time series? Am I right in assuming that only complete time series were permuted, not individual values in the time series?

• Fig. 2: I am not sure that Fig. 2 is really needed. To me as a reader, the only relevant information is the likelihood of obtaining the correlations by chance, which is mentioned in the text; the full distribution is not so interesting, and the differences between the blue, red, and black lines are anyway hard to grasp. While I take no issue with this figure, I believe that it could be removed without loss of information; however, I would like to see the likelihood to obtain the correlations for the net feedback parameter by chance in the text, I only found this information for LW and SW

• l. 150: Given that the first term is 0.43 and the last one is -0.72, does that mean that the internal SW feedback outperforms the internal LW feedback as a predictor for the forced LW feedback (by having a strong anticorrelation)? I find that interesting.

• l. 174 – 175: So if the SW is the strongest contributor, that means that it comes down to clouds (unsurprisingly). Do you think the poor model representation of clouds is a problem for that?

• l. 182: Models have no measurement uncertainty, but EBAF does. Is the uncertainty that arises from the satellite measurements (and also from the temperature data, but I assume that will be less important) taken into account? Would it affect the estimate of ECS or is it too small to make a difference? When combining the measurements from CERES and ERBE, is it problematic that the satellite changes, e.g., are there inconsistencies or steps?

• l. 187: The values are almost all well below 1 %. Doesn’t that mean that less years might also be enough, if we think that, e.g., 5 % would be sufficient?

• Fig. 3 caption: Unclear what is meant by “n – 2014”, what is n here? Should I read it as “n to 2014” or “n minus 2014”?

• l. 194 – 195: The suggested approach here is to wait for new satellite observations, but by then we will also have longer historical simulations. Can’t we just run your analysis on the historical simulations again in 14 years, circumventing the whole problem of using the emergent relationship from one period with observations from another? It’s still an interesting question to ask, but I don’t see the practical necessity to use the “old” emergent relationship 14 years from now

• l. 206 - 216: This seems to be in disagreement with the results of Fig. 4 (d). In Fig. 4 (d) you show that when taking at least 40 years, it doesn’t matter which period one picks, λ_it will always be the same. So λ_it does not depend on the chosen period if the period is long enough. λ_ab obviously doesn’t depend on the chosen period either. So how can the relationship between λ_it and λ_ab depend on the chosen period (that’s what I read from Fig. 4 a and b)? I have a hard time reconciling this. In addition, Gregory and Andrews 2016 (https://doi.org/10.1002/2016GL068406) show that historical feedback has varied quite a bit, although they use shorter than 40-year periods for their regression.

• Fig. 4 (a) and (b). How can the starting year be 1980 and higher for 51-year periods?

• Does it surprise you that the relationship between λ_it and λ_ab varies strongly in time?

• l. 250 – 252 and Fig. 5 (a): +/- 2 W/m^2 seems not negligible compared to interannual variability of global-mean TOA flux, which I would expect to vary by less than 10 W/m^2. How can it be that the correlation with CERES-ERBE is still so high (0.99)? It means that 98% of the variance of the ERA5 feedback parameter is explained by CERES-ERBE, so only 2 % is left for the error, which seems low given that the error gets up to +/- 2 W/m^2.

• l. 277 – 279: I don’t understand the method here. A probability density function of which quantity? What values are sampled from this distribution? I had expected one value for λ_it from ERA5, obtained from regressing over the 40-year period, not a whole distribution. What am I missing? This seems like a central point of the paper and maybe deserves another sentence or two to clarify the method.

• Is there a reason for presenting the results from this analysis as small insets in Fig. 1? It seems like one of the main outcomes of this paper is hidden in a small inset. If showing it in Fig. 1, I would prefer the y-axes of the main plot and the inset to be aligned.

• l. 296 – 301: The list of limitations seems short. In addition to my questions about the pattern effect potentially limiting the results of this study, I think it may be beneficial to discuss further limitations. In particular, the emergent relationship is obtained from model simulations using models, hoping that this relationship would translate to the real world. However, most models that contribute to this relationship simulate λ_it values way outside the observed range (see Fig. 1 f). Could this limit the results?

Minor comments:

• l. 72 – 75: the half-sentence “incorporating a more extensive…” appears twice

• l. 161: The use of the word “assuming” makes sense here, but made me stumble, because it sounds like it’s a prerequisite to run the hypothesis, when it’s actually rather the null hypothesis; “testing for” or something similar would have been clearer to me

The authors investigate the relationship between internal variability feedbacks and forced climate feedbacks across a range of CMIP6 models. They explore the feasibility of using this relationship, along with observed internal variability feedback estimates derived using CERES, to establish an emergent constraint on Equilibrium Climate Sensitivity (ECS). The authors find a robust relationship between internal variability and forced feedbacks, particularly for shortwave and longwave components, whereas the relationship seen for the net feedback is weaker. To address this, the authors explore how the relationship strengthens over longer time periods (50 years). To provide an estimated constraint on ECS, the authors combine satellite observations with a reanalysis dataset to provide an observed estimate of internal variability feedbacks. However, in order to provide a constraint based on observations only, continuous satellite observations until the mid-2030s would be necessary.

I found this paper enjoyable to read and I believe it would be a useful addition to the literature in this field. I have one major comment and a number of minor comments.

Major Comment:

The authors suggest that the relationship between internal variability feedback and forced feedback could be used as an emergent constraint on ECS. However, the utility of this relationship could be challenged were there to be a bias in modelled estimates of internal variability feedbacks compared to observations.

Armour et al. (2024) investigated the relationship between historical temperature trends and ECS, showing that this relationship was not suitable for use as an emergent constraint due to a known systematic bias in modelled estimates of historical temperature trends.

They show that since coupled climate models do not simulate observed temperature patterns, modelled historical warming was systematically warmer compared to observations.

Would the results of Armour et al. (2024) impact the conclusions reached in this analysis? Would this suggest that there may be a systematic bias between observed and modelled internal variability feedbacks due to different SST patterns?

For example, if AOGCMs are biased in their simulation of SSTs patterns and feedbacks due to internal variability, then it is plausible that this biases the emergent constraint with long term feedbacks proposed here.

Either way, I would expect some discussion on the limitations and potential for biases in the results.

Minor Comments:

Line 2-3 – Aren’t the changes in top-of-atmosphere flux in response to surface temperature changes how we often define feedbacks in general (not just internal variability feedbacks). Could the definition of internal variability feedbacks and forced climate feedbacks be more explicitly defined?

Line 50 (and in the introduction in general) – I think it might be beneficial to formally define somewhere in the introduction what is meant by forced feedback and internal variability feedback.

Line 69 – Could the historical and amip experiments used be more clearly defined.

Line 82 – “TOA flux anomalies” – Could the authors write “R” given they have shortened surface temperature anomalies to “T”.

Line 84 – Could the authors expand on how the historical members are detrended?

Line 85 – “various” – Could the authors be a bit more specific?

Line 91 – “the transformed datasets” – It isn’t completely clear what datasets are being referred to here.

Line 81 Paragraph – I think in general, if this paragraph could be re-written to be much more thorough with the details it would help. Further questions I am left with are… How is F calculated in order to calculate the lambda in the historical experiments? Is the idea that the internal variability feedbacks have no forcing effecting them? And if so, how is this achieved given there is forcing over the historical period? Is this why the timeseries have been detrended? If the detrending has had a linear trend removed, given the historical temperature and flux timeseries’ are often highly non-linear, is this definitely an appropriate method? Would that leave an imprint of the forcing still in the timeseries?

I think this paragraph was the main unclear bit in the paper for me.

I was also curious about whether this is a different method compared to that used in Uribe et al. 2022? (i.e. the use of GLS). Has that contributed to the slight change in the results?

Line 125 – This isn’t completely clear what has been done here. How were the datasets randomly permuted?

Figure 3 – All text in Figure 3 is very small and smaller details are rather hard to read. Could the authors increase the font size and perhaps consider re-arranging the subplot to help make it more readable.

Figures in general – Although the other figures are not as hard to read as Figure 3, some may benefit from larger text. Figure 5 is an example of this. Figure 5c also has the legend partially obscured by some of the lines in the plot.

Very Minor Comments:

Line 1 – “, crucial climate regulators,” -  I would remove this or restructure the sentence as it is a little unclear whether the authors are describing the act of observing climate feedbacks or the climate feedbacks themselves. Obviously it is the latter, but I kept reading it as crucial climate regulators is not feasible. – This is a very very minor comment, but I think it would help make the first line of the abstract more punchy.  

Line 85 – “However” – This doesn’t seem like quite the right word, “however” introduces a statement that contrasts or seems to contradict something. Would saying instead “Here, it is crucial…”. Again, a very minor comment, but it stood out to me.

 Line 91 – “a OLS” –> “an OLS”.

Armour et al. (2024) - https://doi.org/10.1073/pnas.2312093121