Allen et al. assess the impact of methane (CH4) shortwave absorption for the increase of CH4 concentration from pre-industrial to present-day conditions.

The study builds on previous work (Allen et al., 2023) which has quantified the impact of CH4 shortwave absorption for idealized CH4 perturbations (2x, 5x, 10x pre-industrial CH4). The present study extends the analysis by explicitly simulating the impact for the present-day CH4 concentration, which corresponds to an increase of 2.5x pre-industrial CH4. Consistent with the 2x, 5x, 10x CH4 experiments, the present study finds that shortwave absorption of methane significantly mutes the effect of its longwave absorption. The study extends the analysis by an assessment of the energy budget and by comparing the effect of methane shortwave absorption to the effect of CO2 shortwave absorption.

The results are presented in a clear and understandable way. In my opinion it is a useful contribution to the understanding of the role of methane shortwave absorption. And - considering methane’s short atmospheric lifetime – the findings are further relevant for the scientific assessment of short-term climate change mitigation options.

Therefore, I recommend publication after some minor revisions detailed below.

General comment

In my opinion, the paper is clearly written throughout most of the text. However, there are some formulations that might be misleading, especially if used out of context.  At some points, the formulations “negative ERF” or “surface cooling” “under SW absorption” are used. I understand that “SW absorption mutes/offsets the (total) ERF” or “the SW effect/contribution to the ERF is negative” is meant. However, especially the formulation “under SW absorption” might be misleading as it could also mean “total ERF/temperature response if SW absorption is accounted for”. Therefore, I suggest to carefully review the formulations and adapt the text where it might be misleading.

Some examples are:

•    l. 114: “For example, the global mean near-surface air temperature (TAS) response under 5xCH4SW and 10xCH4SW (Figure 1a) yielded significant global cooling at -0.23 and -0.39 K.”

•    l. 273: “This negative rapid radiative adjustment promotes a negative ERF under methane SW absorption. …”

•    l. 297: “.., 2.5xCH4SW yields larger (10-20%) and more negative TOA and surface IRFs, ERFs, and ADJs. The larger negative ERFs (and ADJs) act to promote cooling.”

I think that the SW contribution to TOA IRF (2.5CH4SW) is not even negative, but weakly positive (Fig. 2a)).

•    l. 644: The total rapid radiative adjustment for both CO2 perturbations is negative under SW radiative effects at …”

•    l. 831: “… leading to a negative ERF. 

Specific comments

l. 80: The term “rapid adjustments” is used in the introduction without a detailed explanation, which follows in the Methods section. Please shortly explain the term in the introduction or refer to the Methods section.

l. 159: I assume that the simulations are all “time slice simulation” (=cyclic repetition of the boundary conditions every year). This is not explicitly stated.

l. 209: Here an explicit description how the surface temperature driven feedbacks (e.g. Fig. 5) are calculated is missing. I assume that they are also calculated using the kernel method, but with the climate variable from the coupled ocean experiments. The radiative effects of the slow response are then presumably calculated as difference between radiative effects of the fast and total response?

Section 3.4 /Fig. 5:

•    The second paragraph (l. 443-455) might be moved to section 3.1 as only the rapid adjustments are discussed.

•    The radiative effects of the total and slow response are not shown for CH4LW and CH4LW+SW. A figure similar to Fig. 2 b) could be added in the supplement as comparison

Section 3.5.: 

I am a bit confused about the sign convention in this section, which makes it difficult to follow the discussion. Could you give more detail on how to calculate LWC and SWC? Do they represent the divergence of LW/SW radiative fluxes in the total atmospheric column (=loss or gain of radiative energy of the total atmospheric column)?

If yes, I would presume that SWC would lead to energy gain (=warming) for reference conditions as the net downward SW flux at TOA is larger than the net downward SW flux at the surface (see e.g. Fig. 7.2 in IPCC-AR6, The Physical Science Basis). The LWC should lead to energy loss (=cooling) for reference conditions as the net downward LW flux at TOA is more strongly negative than the net downward LW flux at the surface, is this correct? The combined effect of LWC and SWC would be cooling (=net energy loss) as the absolute value of LWC is larger than SWC.

Does a positive LWC / SWC represent cooling (= net energy loss) or warming (=net energy gain)?

l. 850: It might be worth mentioning here that chemical composition changes of O3 and stratospheric H2O also affect the temperature response and thereby the static stability in the upper troposphere and stratosphere (see e.g. Winterstein et al, 2019, their Fig. 8; https://doi.org/10.5194/acp-19-7151-2019; for the temperature response induced by O3 and H2O changes in the stratosphere). Could this affect the cloud adjustment processes?

Typos / technical corrections:

l. 74: Etminan et al., 2016 (misspelled)

l. 94 : “… isolate the effect of …” 

l. 129: estimates (plural)

l. 149: “targeted methane-only equilibrium climate simulations”- This implies simulations perturbed by methane only, but you also conducted CO2 experiments.

l. 217: I assume it is 5% of ERF?

l. 325: Double mentioning of word correlation: “Correlations between … are significant.”

l. 352: Should the unit of static stability be “K/km”?

l. 471: Avoid line breaking between - and corresponding number (-0.31 Wm-2).

Captions of Supplementary Fig. 1, 4 and 5: “Total climate responses are estimated using from coupled ocean-atmosphere CESM2 simulations.” – “using data from coupled ocean-atmosphere simulations”

Captions of Supplementary Fig. 2 and 3: “Annual mean global mean spatial fast responses”: The data do not show the global mean, but the spatial distribution.

This is a valuable paper that makes good progress in understanding how radiative adjustments and responses vary according to the vertical profiles of short-wave absorption. It will certainly be suitable for publication after addressing the issues below.

This study uses the terms “fast” and “slow” responses, and seems to implicitly link the two in suggesting that the slow response is in some sense an extension of the fast response (for instance in the first paragraph of section 3.3). This is a different framework to that of the 6th Assessment Report of IPCC Working Group I (AR6), which used the concepts of “adjustment” to an imposed forcing and a radiative “response” to a global mean temperature change (GSAT) e.g. their Box 7.1, Equation 7.1: Delta_N=Delta_F+alpha*Delta_T. An assumption of AR6 is that the ”response” is almost entirely a function of GSAT, and is largely independent of the characteristics of the imposed forcing, whereas in this study there seems to be an implication that the response (“slow response” in this paper) does depend on the characteristics of the imposed forcing. The paper needs to explicitly acknowledge this difference in framing compared to the IPCC and state whether their results imply the IPCC assumption of radiative response being a function solely of GSAT is overly simplistic.

To aid the above discussion it would be useful to also present the radiative responses in figures 5 and 10 as feedback terms by dividing by Delta_T, and compare CH4sw and CO2sw. Tables of Delta_N, Delta_F, Delta_T and alpha should also be presented (either in the main text or supplement) for all the experiments (CH4, CO2, LW+SW and NOSW) to help understand why the SW effect contributes different percentages for ERF and Delta_T.

In a similar vein, the atmospheric energy budget is often presented as L*Delta_P = k*Delta_T-Delta_F(atm)-Delta_SH (e.g. Thorpe and Andrews 2014, MacIntosh et al. 2016), i.e. separating out the Delta_T contribution to LWC+SWC. Where the response term k* Delta_T is again assumed to be independent of the characteristics of the imposed forcing. It is not quite clear from the text (section 3.5) whether the different forcing characteristics lead to different k*Delta_T responses. Is k constant? As with the TOA budget, it would be useful to have tables of Delta_P, Delta_T, Delta_F(atm), Delta_SH, and k for all experiments (CH4, CO2, LW+SW and NOSW) , not just those in figure 6. This would help understand the percentage contributions of SW and LW effects.

The term “feedback” is conventionally (e.g. AR6) used to describe the radiative response to a 1 K change in GSAT in W/m2/K, whereas in this paper it is used as a synonym for the radiative response itself in W/m2. This could lead to confusion for readers, for instance section 3.4 refers to “negative feedback” several times for processes that amplify the original signal and would conventionally be described as “positive feedbacks”.

Figure 5 shows that the TOA radiative imbalance increases once the ocean is allowed to respond. This is contrary to expectations that the radiative response to the temperature change should be such that it brings the system closer to radiative balance until it reaches equilibrium. If the TOA imbalance is increasing this will imply that the climate system will continue to cool indefinitely without reaching equilibrium. The overall climate feedback term (which should be calculated) is a negative flux change divided by a negative temperature change and is therefore positive and would lead to a snowball Earth  which seems unphysical. This concern needs to be addressed by the authors. This may come about because the ‘SW’ simulation is not carried out explicitly, but as the difference between the LW+SW and NOSW simulations. The time evolution of the net TOA imbalance over the 90 years of the simulations needs to be plotted to understand what is happening.

The 90 year simulations will not be long enough for the full climate response to manifest itself (they obviously have not reached radiative balance). This should be discussed. It is likely that with a coupled ocean the interannual variability will lead to high levels of uncertainty in the calculations, even with a 40-year average. A longer average or a number of ensemble simulations might be needed to reduce this. Uncertainties should be quoted on all values and should be presented on the bar graphs.

It is not obvious that it is necessary to discuss in such detail the comparison between 2x and 2.5x CH4. I understand that part of the motivation for this study was to understand why the 2x CH4 behaved so differently in A23 compared to the larger perturbations. However, for a reader that hadn’t been familiar with the A23 discussions the comparisons between 2x and 2.5x are likely to distract from the main messages. Could this be moved to the supplement?

The qualitive comparisons between CH4sw and CO2sw (particularly the height profiles) are very informative, but the quantitative discussions of percentage offsets are less useful. The SW component of the forcing is much larger for CH4 than for CO2 so obviously it will have a much larger percentage offset irrespective of the difference in height profiles.

Line 2: From section 3.3 the precipitation effect isn’t significant.

Line 24: This sentence needs to be rephrased to reflect that the precipitation effect isn’t significant (line 407).

Lines 43-45: This sentence needs to be rephrased to reflect that the precipitation effect isn’t significant (line 407).

Lines 48-52: These two sentences seem to imply that the difference between methane and carbon dioxide SW effects is mostly due to the vertical profile, whereas the main difference is simply that carbon dioxide absorbs less strongly in the SW compared to the LW.

Lines 132-135: If the linear fits go through zero, then the percentage offsets should be the same at any point on the line. By zooming in repeatedly on figure 1(a, b) I was able to see that the lines don’t go through zero. This can’t make sense since zero change in CH4 must give zero change in Delta_T or Delta_P. Hence this disagreement is purely an artifact of the fitting. Note that in line 418 there is a suggestion of a logarithmic relationship, which would mean that the linear fits in figure 1(a, b) aren’t appropriate anyway.

Lines 223-226: There needs to be some justification provided as to whether these time periods are sufficient.

Page 7-8: The comparisons to 2xCH4 just add a lot of extra values and don’t add any extra science. The 2xCH4 values from the text, and fig 2(c,d)  could be provided in the supplement for anyone who wanted to look them up.

Lines 304-324: Comparisons with 2xCH4 aren’t needed.

Line 353: Explain how this lower-tropospheric stability is defined/quantified.

Line 355-356: Would it be better to say that “the increase in low cloud cover is consistent with the increase in lower-tropospheric stability” rather than the other way around?

Section 3.3: I think this would be much clearer to understand if the response to surface temperature (“slow” in the notation of this study) were isolated from the total response. Showing just the sum of the adjustment and the response risks conflating the two and implying that they have a common cause. If the authors do wish to make the point that the adjustments and responses are more closely linked than in the IPCC AR6 framework they should make the point explicitly.

Lines 386-389: It doesn’t really add scientific value to compare the magnitude of the lower tropospheric temperature adjustment to the total response since the first is strongly constrained by the fixed SST.

Lines 398-399: The uses of “muted” and “augmented” imply again that the adjustments and responses are more closely linked than in the IPCC AR6 framework. If this is the intention this point should be made explicitly

Line 400: An example of the possible confusion by presenting the total rather than separating out the response to temperature comes from the sentence “The total response of “CONCLOUD is generally similar to the fast response …” At first reading I took this to be that that the temperature-driven response is similar to the adjustment, then I realised that for the total to be equal to the adjustment, then the response has to be zero.

Lines 408-410: It appears that the ratio of temperature change to ERF is much larger (-0.1/-0.1) for the SW than the LW (0.35/0.53). And this is the reason a larger fraction of the warming (29%) is offset compared to the forcing (19%). This should at least be commented on. Does it appear that the climate system has a greater climate sensitivity to the pattern of forcing from the SW? How robust is this? Using an uncertainty in the temperature of +-0.04K (from line 42, but should be quoted in this section), the ERF and warming fractions are consistent within uncertainties.

Line 411: Presumably this 66% is not significant if the change in precipitation is not significant.

Lines 412-417: I’m not sure the discussion of the warming patches is useful since they are unlikely to be robust.

Lines 418-428: The methane forcing is typically assumed to vary with the square root of the concentration (e.g. Etminan et al. 2016). This paragraph asserts that the variation is logarithmic. Are the uncertainties small enough to discount the square root dependence? Is there a physical reason why it should be logarithmic? Are the SW bands nearer saturation than the LW ones?

Line 458: The total feedback is positive (which is in itself worrying) and these terms make a positive contribution to the feedback (since they are negative radiative responses to a negative temperature change).

Line 462: In IPCC terminology these are “responses” not “adjustments”, again they are positive responses that contribute a negative feedback to an overall positive total feedback.

Lines 464-490: This paragraph compares the “fast” and “slow” responses, but under the IPCC framework there is no link between “adjustment” and “response” (apart from through global mean temperature). This leads to some confusing statements. For instance “… lack of an increase in upper-tropospheric heating rate” makes it sound as if something is missing in the response, but since the mechanisms are completely different there is no connection between the impact of an imposed forcing and the response to a global mean surface temperature change.

 I think in all cases “feedback” needs to be replace with “response”. This needs to be checked.

Lines 492-494: is the difference between 19% and 29% significant? The 66% precipitation increase is not significant.

Lines 503-549: In order to follow the discussion in these paragraphs, it would be very useful to have a table of all the numbers for figure 6, with the sum of the components (which presumably should be exactly equal to LcP if energy is conserved in the model). Does the hydrological sensitivity of the “slow” mode here agree with e.g. Flaschner et al. 2016 of ~2.2 W/m/2/K?

Lines 560-569: It should be made clear here that the difference in behaviour between BC and CH4sw is that BC has a positive TOA ERF whereas CH4sw has a negative TOA ERF. However both species have a positive atmospheric ERF.

Lines 575-582: I find this discussion of the QRS profile rather confusing. It is the total atmospheric forcing (i.e. difference between TOA and surface) that matters, the vertical distribution is not important. It may be the authors are trying to make the point that the atmospheric forcing from CH4sw has positive and negative regions that the total forcing is less than if it were uniformly positive like BC.

Lines 583-585: It is not made very clear here why the different vertical heating profiles of CH4sw and BC should lead to different ERFs. I think the argument from section 3.3 is that because the QRS for CH4sw is negative in the lower troposphere the low cloud adjustment is sufficiently negative to make the total ERF negative, whereas because the QRS for BC is positive in the lower troposphere there isn’t such a negative low cloud adjustments and the overall ERF is positive. If this is indeed the argument, it should be stated more explicitly.

Section 3.6: Uncertainties need to be provided on all values here in order to be able to work out whether similarities or differences with CH4 are significant.

Lines 714: I don’t quite see how the vertical temperature profile is not consistent with the QRS profile for the total climate response.

Lines 725: It is interesting that the temperature responses to CO2sw and CH4sw are similar (~ 1K per W/m2), and are higher than for the CH4lw (0.7K per W/m2). The response for CO2lw should be provided as well. Are these increased climate sensitivities for SW significant? Is there any physical explanation?

Lines 732-735: Again, it is not quite clear whether this is trying to suggest that the slow cloud response is an amplifying effect particular to the SW forcing (and is similar for CH4 and CO2), rather than the slow cloud response being common to any global mean temperature change, and in these cases happens to add to the adjustment.

Lines 736-748: I’m not convinced this discussion comparing the SW and LW effects adds anything useful. CO2 has a much smaller SW component.

Lines 782-797: I appreciated the authors wanted to understand their A23 results, but this discussion of simulated vs inferred is likely to be of little interest to most readers. It should be moved to the supplement along with figures 1(c-e).

Lines 816-820: For the fast responses it is only the integral of the QRS profile that matters, not whether it is positive or negative at particular levels. The difference in behaviour between CH4sw and BC comes from the different signs of the global temperature response which is driven by the ERF. I think the point is that the negative QRS in the lower troposphere leads to a negative low cloud adjustment for CH4sw and hence negative ERF, whereas for BC the positive QRS in the lower troposphere leads to less low cloud adjustment so the ERF is overall positive. This should be clarified here.

Lines 829-846: I don’t think the quantitative comparison of the various percentages of offsets between CH4sw and CO2sw is a key conclusion since CO2sw is only a small component of the CO2 forcing.  Rather, the qualitative understanding of the impacts of different QRS profiles on adjustments and precipitation for CH4sw, CO2sw and BC is an important finding and should be expanded on explicitly here.

Lines 864-871: Note that the IPCC AR6 CH4sw values are based on 4 models, one of which is CESM1. Therefore care needs to be taken when comparing with IPCC not to compare the model with itself.

Line 817: The IPCC AR6 estimates an overall increase in methane ERF from including SW absorption. There is a +0.12 W/m2 increase in SARF (from Etminan et al. 2016 and largely due to including SW absorption) and a -0.08 W/m2 decrease due to cloud adjustments from Smith et al. 2018, leaving an overall increase of +0.02 in ERF from including SW. Hence I think this study would lower the methane radiative efficiency. The impact of the adjustments on the Etminan radiative efficiency could be estimated here by adding the adjustments from figure 2, assuming that the Etminan value only includes stratospheric temperature adjustment.

Lines 878-900: I don’t think the emission-based discussion is useful here as it detracts from the key messages on adjustments.

Line 902: The uncertainty on this 30% needs to be added. The smaller decrease (19%) in ERF needs mentioning too, since it is not obvious why this is amplified in the temperature, and whether this amplification is robust.