We appreciate the comments offered through the public comment on our manuscript.  The core suggestion of the reviewer concerns our choice of scenario (SSP3-7.0) and our choice to run our simulations through the year 2100 so as to consider variance changes at the end of the 21^st century, rather than choose the near-term years 2040 or 2050.   Our decisions in these matters were anchored in community-based decisions as reflected for example in the O’Neill et al. (2016) ScenarioMIP paper, that suggested SSP3-7.0 for large ensemble simulations.  And more broadly, we chose to follow in most ways the CMIP6 protocols that were developed through broad community decision-making over the last 5 years.    We wish in no way to denigrate or dissuade research focusing on nearer-term changes, nor does our work endorse or “choose” most likely outcomes of political decisions or put our money on the most likely scenario for future change.  The O’Neill et al. (2016) study was quite specific in its recommendation that as a relatively strong scenario, SSP3-7.0 offers relatively strong forcing, with this being appropriate for studying changes of variance over the 21^st century.  We’re sorry for any misunderstandings in this regard.  In the revised text, we will state more clearly how our model configuration was chosen within the context of broader CMIP6 efforts.

As a matter of procedure, we would encourage the reviewer to participate in the development of protocols for CMIP7, as this is where the protocols that shape studies such as ours are developed and expressed to the climate community.   To reiterate, the interests and questions raised by the reviewer are clearly of value and interest for enhancing both public awareness and policy.  But procedurally the most constructive way to bring such concerns to the table may not be through arguing posteriori that submitted manuscripts have illegitimate priorities for their chosen timescales (is any timescale illegitimate in climate science?), but rather in shaping community priorities through open processes. 

We thank the reviewer for their careful reading of the manuscript.  In our responses detailed below to the review, we have dedicated our attention wherever possible to the suggestion that we take the opportunity to provide an interpretation of our findings. To this end, we have emphasized in our responses where we plan to anchor the descriptions of our large ensemble behavior to mechanisms and model behaviors identified in previous studies. 

Our detailed responses are below. For purposes of clarity, we have put the reviewer comments/questions in italicized text, and responded in plain text.

SPECIFIC COMMENTS

ll 33-37: I find a bit limiting the notion of fluctuations as “characterized by spectral variance peaks superimposed upon a broad noise background”, as I think it does not entail the possibility that modes of spatio-temporal variability are in fact influenced by the “noise background” itself. Especially when one deals with processes that have clearly non-Gaussian PDFs, as in the case of this analysis, it is worth mentioning that at least multiplicative noise processes (and externally-driven changes therein) can alter the modes of variability through nonlinear interaction (e.g. Majda et al, 2009;  Sardeshmukh and Sura, 2009; Sardeshmukh and Penland, 2015). 

We thank the reviewer for raising this point.  Indeed the role of multiplicative noise in affecting variability on a multitude of timescales is well established in the literature. The references suggested by the reviewer will be included in the revised draft, in addition to references to Levine and Jin (2010; JAS) and Jin et al. (2020, Simple ENSO Models in AGU monograph on El Niño in a changing climate).  To our knowledge the Mueller paper is the first that describes the influence of multiplicative noise on second- and third-order cumulants and spectra in the context of the stochastic climate model.  The other papers touch on the highlight the role of multiplicative noise in generating ENSO characteristics.

We will further revise the text by adding the following sentence:  “The spectrum of observed regional-to-global climate fluctuations exhibits spectral variance peaks and a broad noise background (Hasselmann, 1976; Franzke et al., 2020). Spectral peaks can emerge from a range of mechanisms, including astronomical forcings and internal climate instabilities, such as for ENSO.  Moreover, these distinct features can be further influenced by climate processes acting on different timescales.  Examples for this type of nonlinear “timescale interaction” are multiplicative (state-dependent) noise (Mueller, 1987; Majda et al., 2009; Sardeshmukh and Sura, 2009; Sardeshmukh and Penland, 2015; Jin et al., 2007; Levine et al., 2010; An et al., 2020; Jin et al., 2020) and combination model dynamics (Stuecker et al., 2015).

ll 62-64: while I find that mentioning Milinski et al. (2020) objective algorithm for the detection of the required LE size is appropriate, I think that with the algorithm being model-dependent, it should be acknowledge that their conclusions do not a priori apply here. Possibly a sampling over the pre-industrial simulation, using it to test the internal variability associated with ENSO, would hint at the number of members that is actually required (even though one would have to assume that the same holds when the SSP3-7.0 forcing is applied). 

The point of the reviewer regarding the model-dependence of the Milinski et al. (2020) study is well-taken, and this question is the subject of an independent study with CESM2 led by one of our coauthors, Tamas Bodai.  It is indeed not possible to project the necessary ensemble size in a model based on findings from another model configuration, and there are other issues that complicate the idea of prescribing a general rule ensemble sizes required for an experiment.  As for the generic idea of an ensemble-size dependence o f detectability and the accuracy of identifying forced changes, the following figure considers variance changes for Niño3 SST following the suggestion of the reviewer:

In the figure, rho denotes the detection rate, calculated with a bootstrap mean over 1e3 bootstrap samples, and F refers to the F-test for the slope, concerning whether it is significantly non-zero at the 95% significance level.  HAC refers to a technique that considers heterscedasticity and auto-correlation – which are themselves in fact not detectable here, hence the agreement between rho_F and rho_F,HAC .  Thus the 20^th century changes in the model are already detectable with 20 ensemble members.

The study of Milinski (2020) is not concerned with detectability, but rather with the accuracy of large changes, and this is addressed by the yellow and purple lines in the figure. alpha is the temporal slope of the ensemble standard deviation, and the purple line indicates the best estimate from the 100 ensemble members.  q_97.5 and  are the 97.5^th quantile (corresponding to the upper (u) bound of the 95% confidence interval) and the standard deviation over the bootstrap samples, respectively, with the relative errors/”variance” plotted.

ll. 106-107:  the choice of the section of the pre-industrial run, where the model drift is particularly small, should be better justified.  The internal variability of the model might be influenced by the presence (or absence) of such bias, and it would be relevant to assess how relevant this impact is.

In the revised manuscript, we will provide a clearer description of model drift over the span of the initialization dates from the pre-industrial control run.  In the CESM2 presentation paper of Danabagoglu et al. (2020), Fig 6. Showed the TOA energy imbalance for the pre-industrial run over years 1-1200, revealing minimal drift by year 1000.  Additional extensive diagnostics by NCAR scientists identified minimal drift for the AMOC, and for upper ocean heat content over the North Atlantic and Southern Ocean over years 1000-1300. 

ll 108-116:  I am a bit puzzled by the choice of the initialization dates for the ensemble.  80 members are initialized with 4 initial dates (sampled according to the phase of the AMOC; maximum AMOC, minimum AMOC, ascending AMOC, descending AMOC), then slightly perturbing these initial conditions (20 members per date); for the additional 20 members, initial dates separated by 10 years were chosen.  I find hardly justifiable that the members are to be considered as independent, and identically distributed, and that as such, conclusions can be drawn about ensemble mean moments of the distribution.  I acknowledge that, as the authors state at ll. 122-123, “further quantitative exploration of the specific duration over which initial condition memory is retained is the subject of a separate ongoing study”, but I see two issues in this choice of the initial dates:  1.  Members chosen according to AMOC phase are not uncorrelated by construction; 2. When it comes to the internal variability of the ocean, it is quite unlikely that 10 years are a sufficient decorrelation time.

We were not sufficiently clear in our submitted manuscript about issues surrounding the initialization strategy, through a mix of macro-and micro-perturbations.  It was not our intention to argue that the initialization procedure for CESM2-LE produces members that can be considered as independent, and we should have stated this more clearly, we apologize for the misunderstanding.  Our analysis with internal variability is primarily focused on the post-1960 period, so more than a century after the 1850 initialization time for all members.  In order to clear up any potential confusion, in addition to more detailed text clarifying the initialization procedure, we will provide in the revised manuscript both a quantification of the decorrelation timescale for the AMOC, as well as a timeseries figure showing the evolution of AMOC transport over the late 19^th century for the 4 sets of micro-perturbation runs, illustrating the timescale over which initial condition memory is lost.

This two-panel figure shows the evolution of AMOC for (top panel) individual ensemble members over 1850-2000, and (bottom panel) ensemble means for the four micro-perturbation groupings as well as the ensemble mean of the macro-perturbations, all considered at 26.5°N.  By the year 1900, the bottom panel indicates convergence in the ensemble mean groupings.

This is consistent with the autocorrelation for the (detrended) AMOC calculated using years 401-2000 from the pre-industrial control run (piControl), as shown for both 26N and 45N in the above figure. This is consistent with our interpretation that the analyses in Fig. 2 and Fig. 4 occur well beyond the time when initial condition memory is important.

ll 130-136:  I do not think that enough evidence is here provided that the two ensembles with different biomass burning can be assumed as being (or not being) part of the same population.  An assessment through statistical tests (e.g. Mann-Whitney?) would here support such an argument.

We fully agree with the reviewer that during the period of biomass burning perturbations (1990-2020, effectively) the full suite of 100 members should not be assumed to be part of the same population, but rather considered as two sets of 50 members.  This is what motivated our Supplementary Fig. 2 in the submitted draft.  There are two new manuscripts under development led by ICCP scientists (coauthors on this study) that deal explicitly with the impacts of biomass burning on the climate state. For the surface temperature, sea ice, and precipitation the response is only significant over the 1990-2020 interval of the biomass burning perturbation itself.  This is the reason why we chose the intervals 1960-1989 and 2070-2099 for our emphasis on changes in variance, as the first of these is prior to the biomass burning perturbation, and the second is 50+ years after the perturbation.