This paper analyses the transition to superrotation in an idealized GCM as a function of the thermal Rossby Number that is controlled by varying the radius of a planet. The focus, in particular, is on the early warning signs (EWS), including amplitude and autocorrelation of the noise before the transition. The authors present an expansion of the concept of EWS to multi-variate state space. I find the subject interesting, the analysis well done, and the paper well written. I make some minor suggestions below, and I recommend accepting the paper subject to minor revisions.

Specifics:

It would be helpful to mention in the introduction that superrotation does not occur at the surface in this study, which is consistent with related recent studies. I believe there is a recent paper by Caballero and collaborators where they try to see what might lead to surface superrotation. Such superrotation, which does not reach the surface, may not have dramatic socioeconomic consequences, and it might be good to mention that as well in the introduction and conclusions.

It seems that the analysis of the multi-variable EWS is based on building a reduced-space, EOF-based linear inverse model and then analyzing it following the principle oscillation pattern (POP) approach. The linear inverse model is not explicitly mentioned; I am deducing this from what is written. In any case, the specific methodology should be mentioned using wording that connects the methodology to the existing literature in the abstract, introduction, and conclusions. It would be helpful to the readers if the authors cited previous papers that use POP and linear inverse models in different contexts.

The discussion of the spatial modes at the end of section 6 is a bit of a let-down after the buildup of this multivariate analysis as a main new result here. Is there anything else that can be said?

The paper explains all concepts used very carefully, perhaps even at a somewhat too elementary level at times. Mostly, this is fine, although I would suggest removing lines 373-380 and 390-401, which are just too basic.

Remove the paragraph on lines 560-567, which seems irrelevant to this paper.

The definition of tipping points in the second sentence of the paper is vague. I realize the authors have been using this definition in the past. On the positive side, I note that the paper carefully discusses the different types of bifurcations (noise-driven, rate-driven, equilibrium) at a later point. Despite that, this vague definition seems difficult to digest for this particular reviewer. Perhaps the authors can simply say, "We define tipping points as...". 

I forget if the papers mentioned on line 72 (Huang et al., 2001; Caballero and Huber, 2010; Mitchell and Vallis, 2010) examined a gradually increased CO2 to look for a transition or just simulated at high CO2. If the latter, they didn't look at the actual transition, so a slight rewording of the sentence may be needed.

Line 75: is -> does

I suggest eliminating Figure 6 as it is repeated in Figure 7.

Around line 300: I agree that the differences between the results for the increasing and decreasing parameter value are not significant and may be due to the short time series and are not a sign of bi-stability. The authors do say so eventually. Perhaps they can make it clear as soon as this result is presented.

Figure 11 needs some work: why are dotted circles drawn around the spheres? Remove them (colored titles are sufficient) to allow increasing the sphere size instead; eliminate white space, make middle panels larger; find a different way to present the black dots in the middle panels that are currently just too messy; reformat titles to be over two lines to allow increasing the size of graphics elements and eliminate white spaces; add (a), (b), etc. to the different panels and refer to them in the caption.

Figure 12: make graphics/spheres much larger by reducing white spaces.

Overview:

This paper examines the transition to superrotation in an atmospheric dynamical core

with Held-Suarez forcing. The transition to superrotation is induced by changing the

planetary radius, following previous work. The novelty here is in the application of

tipping-point 'early warning signal' diagnostics to the transition. While the general

idea of the paper is of some interest, it seems to me that the specific way it is set up

and developed in this paper misses the mark. To be more specific, I can think of two

reasons to be interested in EWS of superrotation: (i) in the real-world climate change

context, it is certainly of broad interest to examine methods for early detection of

such a transition in response to increasing CO2; (ii) in the context of atmospheric

dynamics, the EWS approach may give new physical insight into the mechanisms of the

transition, which would be of interest to a broad audience in GFD and planetary

atmospheres.

In its present form, this paper unfortunately does neither of those things: by the

authors' own admission, the modelling setup is not relevant to real-world climate

change, and the analysis is purely empirical and does not give much (or any) insight

into underlying physics. The paper also feels haphazardly written, with long expository

passages covering basic text-book material, and some paragraphs at the end that veer

into theoretical physics language whose relevance is not very clear. There are also some

logical non-sequiturs, many typos and some figures which are hardly legible and not very

informative. As a result, I can't recommend this paper for publication in its present

form. My suggestion is to extend the analysis in the direction of (ii) above, to include

some more material that at least yield some hints as to the physics. I offer some

comments and suggestions below that may hopefully help the authors develop and improve

the paper.

Main comments:

1. The exclusive focus of the paper on a single level, sigma=0.74, seems unmotivated and

gives a sense of cherry-picking. What is special about this level? When this level

transitions to superrotation, at RoT ~ 1, the entire troposphere above it is already

superrotating, as is clear from Fig 2. Wouldn't it make  more sense to focus on the

*first* transition to superrotation, which happens in the upper troposphere presumably at lower RoT?

Does the oscillatory behaviour found here in the lead-up to superrotation also happen at

those levels? I would suggest repeating the analysis of Sec. 4 at various levels, at the

RoT values relevant for transition to superrotation at those levels.

2. The general idea of EWS is that there is an underlying loss of stability of the

system. The paper never looks at the equations of motion and their stability, so this

link is never explicitly made. There is in fact much theoretical work not mentioned here that in

fact supports this superrotation-as-an-instability idea in precisely the context studied

here, for example Wang, P., and J. L. Mitchell, 2014: Planetary ageostrophic instability

leads to superrotation. Geophys. Res. Lett., 41, 4118–4126, Zurita-Gotor, P., and

I. M. Held, 2018: The finite amplitude evolution of mixed Kelvin-Rossby wave instability

and equatorial superrotation in a shallow water model and an idealized

GCM. J. Atmos. Sci., doi:10.1175/JAS–D–17–0386.1, Zurita-Gotor, P., Á. Anaya-Benlliure,

and I. M. Held, 2022: The sensitivity of superrotation to the latitude of baroclinic

forcing in a terrestrial dry dynamical core. J. Atmos. Sci., 79, 1311–1323. The basic

idea is that superrotation arises from wave-mean flow interaction, specifically the

interaction of equatorial Kelvin and Rossby waves that mutually amplify each other (the

Kelvin-Rossby instability) generating a planetary-scale mode that converges zonal

momentum onto the equator and drives superrotation. This happens first in the upper

troposphere near the tropopause, where zonal jets are strongest and yield high

phase-speed Rossby waves which can lock in phase with Kelvin waves. This previous work

should at least be cited and discussed here. More interestingly, the POP analysis

applied here should be able to pick up those Kelvin-Rossby modes, providing an

interesting path to confirming their relevance for the transition beyond what is already

done in the papers of Mitchell and Zurita-Gotor.

3. Different levels in the troposphere are not independent, they are coupled through

momentum transports by the mean overturning circulation (the Hadley cell), among other

mechanisms. It would be interesting to have some idea of how the oscillatory behaviour

found at a single level relates to vertical exchange with other levels, and more

generally with oscillations in Hadley cell intensity. For example, the authors could

examine regression maps of zonal-mean u at one level with that at other levels, and with

the intensity of the Hadley cell.

Line comments:

l.21: It's not clear to me how the quasi-resonance phenomenon counts as a tipping point,

there is no suggestion of a bifurcation in the underlying physical picture described by

the proponents of that theory.

l.23: What specifically are the 'huge impacts' that superrotation would have if it

occurred?

l.28-31: The term 'tipping point' usually refers to a sudden transition caused by a

smoothly-changing parameter crossing a bifurcation threshold. By contrast, (a) and (b)

here refer to noise-induced transitions between metastable states at a *fixed* parameter

setting. So please either give a clear definition of what you mean by 'tipping point', or

remove these two examples, which in any case feel superfluous to the rest of the paper.

l.67: The Caballero and Carlson (2018) paper does not argue that transition to

superrotation is unlikely; it argues that transition to superrotation *at the Earth's

surface* is unlikely. Superrotation in the upper troposphere happens readily in climate

states possible under high-end future climate warming scenarios.

l.146: If zonal-mean u is negative, then Rayleigh damping as specified in Eq 6 will

*accelerate* the zonal-mean wind and act as a *positive* angular momentum flux

convergence, so this argument does not make sense to me. The reasons why it is difficult

to obtain superrotation at or near the surface are examined in detail in Caballero and

Carlson (2018). Please rephrase this section to strengthen your argument. Also, as noted

above, focusing exclusively on this level feels like cherry-picking because it is

influenced by Rayleigh damping, which could affect the dynamics; hence the value of

repeating the analysis at higher levels which are not influenced by Rayleigh damping.

l.192: This describes an Ornstein-Uhlenbeck process. The authors should note that

the noise in this process is internally generated by the chaotic high-frequency

dynamics, and approximating it as white noise is a strong assumption.

Sec. 6.1: This long exposition of the POP decomposition is text-book material and I

don't see its value here, it only dilutes the text. I recommend shortening to a single

paragraph giving a concise, intuitive explanation of POPs, and a reference to a relevant

text book such as von Storch, H., and F. W. Zwiers, 1999: Statistical Analysis in

Climate Research. Cambridge University Press.

Figs 11,12: I don't see the value of using the orthographic projection in these figures,

which doesn't show the full global structure of the modes (so it's difficult to see at

at glance what the zonal wavenumber is, for example). Also, the panels are too small to

see the arrows properly. I recommend re-plotting using a standard cylindrical projection

for ease of comparison with previous work (see main point 2).

l.542-566: These three paragraphs are full of impressive-sounding language, but I don't

see how they are directly relevant to the work discussed here. I recommend rewriting to

make the relevance clearer, or (preferably) eliminating them.

Typos:

l.87: rotating -> superrotating

Eq (8): Should be T_bar, not T_0?

l.210: minimally what?

l.350: This sentence is garbled, please re-write.

The authors explore early warning signals of super-rotation in a GCM, finding that spatial mode decomposition can yield useful information for predicting a transition to the super-rotated state.  The also confirm that standard signals, like lag-N autocorrelation and variance, herald the transition, and explore whether there is evidence for bistability.  The paper is well-written and makes a good contribution to the literature on spatial early warning signals by pointing out the potential value of looking at dominant spatial modes.  I only have a few minor comments that the authors may wish to take up.

1. Regarding bistability, an increase in the skew of a time series may indicate the presence of a nearby stable state (https://link.springer.com/article/10.1007/s12080-013-0186-4), and the fluctuations in Figure 8 seem to show a strong upward skew for R0T near 0.5. The authors could compute skew and see how it compares to lag-1 AC and variance.
2. Further to point #1, since a complex system may transition well before or well after the point where theory suggest to expect the tip, I don’t see why ramping R0T up and then down across the tipping point is a good way to check for bistability. It seems like it would be easier to check through experiments that initialize the system in either a rotated or super-rotated state, for the same R0T, and then study whether it remains in those states.  R0T would be varied across a range.  But perhaps this is not computationally feasible with a GCM.
3. Figure 6: what accounts for the initially high value of lag-1 AC, when R0T is close to zero?
4. Figure 11, 12: A legend for colours on the sphere (windspeed) would be helpful.

Dear authors, 

I have read with interest you paper. The topic is important and I find it useful to look into the connection between regimes of superrotation and indicators of proximity to potential tipping behaviour. I have to say though that I am not convinced by various key aspects of the paper that I mention below. Most importantly, I am particularly concerned by the fact that the paper sometimes seems not to follow a clear logical thread.

1. Introduction

- I think it would be useful to mention explicitly the existence of multiple competing states for the tipping elements mentioned around line 15. It would also important to emphasize that metastability occurs also in very dynamical circumstances very different from the usual scenario, see:

Feudel 2023 https://npg.copernicus.org/articles/30/481/2023/npg-30-481-2023.html

Additionally, when discussing early warning signals, I think that citing the recent paper by Boettner and Boers 2022 Phys Rev Res would be beneficial

- I do not find Figure 1 very informative, it is similar to standard images one can find in many books of mechanics or geophysical fluid dynamics

- Around line 75, the authors introduce the concept of smooth transition to the super rotating regime, differentiating from the abrupt case. Abrupt transitions seem those associated with the kind of tipping behaviour investigated below. Since the authors find a smooth transition, this create a sort of logical non-sequitur in the later part of the manuscript. 

2. Methods

- I do not understand Equation 6 - where are the advective terms?

- Line 130: the author explain that the transition to superstation is achieved for Ro\approx 1. This means, keeping the rest unaltered, considering a value of meridional temperature gradient about 40 times larger than the terrestrial one. This seems to make extremely little physical sense (one would have to consider temperature that cannot be realised by the geophysical fluids). So I am lost at to relevance for the terrestrial circulation. I understand that the authors consider different radii to perform simulations (even if I wonder whether the model behaves consistently well for such altered conditions).

- Eq (8): is it T_0 or \bar{T}? T_0 seems to depend on latitude (Eq 7)

3. Mean Atmospheric State with varying R_{OT}

- I wonder whether Fig. 2 would be more informative if including information on the angular momentum instead dof the zonal velocity - at the end the authors discuss only the properties of the flow at the equator.

4. Temporal Early Warning Signals

The authors describe (lines 165 to 222) the derivation of early warning signals (EWSs) for system characterised by a fixed point. Yet their dynamics is turbulent. In order to construct the EWS, they use as reference the long term average of u (Eq (19)). Assuming that the fixed point and the long-time average are the same thing is a major and critical simplification. 

Additionally, the authors make reference to lag-1 autocorrelation . It is not clear what "1" refers to, in which time units. Additionally, other indicators are much more robust at the lag-1 autocorrelation, like the integrated autocorrelation time.

This part - as well as the related Section 6.1 below - reports - with fairly good degree of clarity - material that has been dealt with in greater generality in Tantet et al, (2018) Nonlinearity, Chekroun et al. (2020) J Stat Phys and Santos Gutierrez and Lucarini (2022) J Phys A, with no restriction on the fact that the reference state is a fixed point. These references should be cited for completeness.

Similarly, these papers also discuss the modes (Sect 6, spatial precursors)associated with criticality as being critical modes of the Koopman operator of the system. In the case of fixed point reference solutions, one finds the special case discussed in this paper.

In any case, In terms of presented results and interpretation, I am not sure why one should expect that the EWSs discussed in this section - which refer to the case of abrupt transitions - should work in the case of smooth transitions. I might be wrong , but I do not find a clear logical thread here.

5. Evidence of bistability

I am a bit of at loss here. The content of the section indicates that there is no evidence of bistability. The title is in my opinion misleading.

In section 6 - mentioned above - the "critical" modes are discussed, and in my opinion the claim that their represent criticalities is not well founded. The relaxation times are of the order of 20 days both for the reference case R_{OT}=0.02 and the case R_{OT}=0.87. So in my opinion the authors are finding "simply" the slowest decaying modes, which, indeed, contain important information on the dominating feedbacks of the system. The reason why the slowest decaying mode is responsible for the variability of the system is presented in Chekroun et al. 2020 mentioned above.