This paper is concerned with the potential of crossing a bifurcation point in the transition from a seasonally ice-covered to a perennially ice-free Arctic Ocean (loss of winter sea ice), and more broadly with the detection and quantification of hysteresis in a dynamical system. This is a topic that has been debated for a while by the cryospheric science community and features interesting nonlinear processes. Therefore I would assess it in general germane to the journal. 

The paper is well written, soundly structured, and clearly illustrated. However, from my reading it suffers from a couple of substantial shortcomings at this point that - in my opinion - would have to be remedied before the manuscript is considered for publication.

I believe the term "rate-dependent hysteresis" is more widely used and more suitable than "transient hysteresis" and I will use it here. 

I think a source of confusion in the manuscript is that the concepts of rate-dependent hysteresis and rate-independent hysteresis (ie., the loop traced by equilibrium states) are not separated clearly enough. It is well known, but somehow muddled at points in the manuscript that there is two distinct types of hysteresis at play: one due to bistability in the system and one due to a transient lagged response (which is the result of the inertia present in any physical system). 

There are well-established methods to probe either. The authors mention some of them but somehow find them lacking. Naturally, the steady-state solutions of a dynamical system can only be approximated in integrations with finite time steps, with the time steps having to become infinitesimal in order to approach the steady state. 

Yet, whether a solution is approximately converged can be tested in fairly straight-forward and well-established ways: for example, as the authors mention, you can take a given fixed forcing level and choose two initial conditions on either side of the suspected stable states (say, very warm and very cold) and run the simulations until you see whether they converge on the same state or not. This avoids complications from the lagged response of the system due to gradually ramping the forcing, which is a separate issue. However, you can typically use the fixed-forcing method to assess how far from the steady-state solution you are in a transient simulation. 

Of course, you can consider the maximum steepness of the hysteresis loop and how it depends on the rate of forcing change (as the authors propose) to assess whether the hysteresis is rate-dependent or not. You could also use a method (which seems to me equivalent and more common) where you consider the range of forcing over which the hysteresis stretches (length of the gray bars in Fig 1a), again as a function ramping rate. If the ramping rate goes to zero and the hysteresis width disappears you'll conclude that the hysteresis is purely rate-dependent and the system is not bistable. 

The method proposed here as I understand it from Fig 3a combines two established approaches: (1) you run your simulations very slowly with different initial conditions in order to find the quasi-static approximation to the steady-state hysteresis loop (or in the case of Fig 3, the location of the bifurcations in Scenarios 1 and 2). (2) You run it faster and look at how the width of the hysteresis loop depends on the rate of forcing change in order to assess the rate-dependence of the hysteresis loop. As far as I understand it, this combined approach may be OK, but I see two issues: (A) I feel it confounds the two issues of rate-independent and rate-dependent hysteresis, rather than separate them clearly. (B) The authors fail to show that this approach is actually computationally advantageous, compared to the standard methods that probe either 1) or 2). How would this proposed approach be implemented in comprehensive GCMs? 

It is further unclear to me what is gained by fitting a seemingly ad-hoc exponential decay equation to match the data points in Fig 3a. 

Some of the lack of clarity here is compounded by ambiguity in the use of the term tipping point: at points it seems that tipping point refers to a bifurcation, at other points it is suggested that the system can feature a tipping point without bifurcation (e.g., l.25). Furthermore, the last paragraph seems to misrepresent the state of scientific debate somewhat: On the one hand, yes, most previous work on this topic is focused on whether or not there is rate-independent hysteresis. On the other hand, I'm fairly certain most authors would readily agree that there would be rate-dependent hysteresis if the climate was warmed quickly and subsequently cooled, simply due to the inertia of the Arctic and the global climate system. Most people wouldn't call this hysteresis I would guess, but rather a lagged response.

Finally, the authors state that they find "transient hysteresis" in all scenarios, and again this mixes the two distinct hysteresis concepts. They really find rate-independent hysteresis in scenarios 1 and 2, and no bistability but a lagged response in scenario 3.

My second main concern is regarding the applicability to the case of winter sea ice. For one, it is unexpected that the authors use the Eisenman (2007) which is from a non-peer reviewed WHOI summer school report. It is my understanding that subsequent versions developed by Eisenman and Wettlaufer (PNAS, 2009) and Eisenman (JGR, 2012) are better formulated variants of this model and would seem a more natural starting point. It seems at least appropriate to justify the use of this model over the later peer-reviewed versions. (I would also urge the authors to summarize the main equations of the model in the main text, in order to make the article more self-contained.) 

Maybe more importantly, the main story of the this paper does not seem to be concerned with Arctic sea ice, but rather with testing hysteretic behavior in dynamical systems. In this regard, the placing of the findings in context of existing literature is lacking: for example, the system of eq 1 has been used to study related questions in many cases, none of which are cited here, which makes it almost sound like the authors suggest this is an original contribution. To mind come the classic textbook by Strogatz ("Nonlinear Dynamics and Chaos", see Ch. 3.6.), Ditlevsen and Johnsen "Tipping points: Early warning and wishful thinking." Geophysical Research Letters 37.19 (2010), and recently Boers "Observation-based early-warning signals for a collapse of the Atlantic Meridional Overturning Circulation." Nature Climate Change 11.8 (2021): 680-688. In the latter text you'll see in Fig 1 that the transient solution continues beyond the bifurcation point before the abrupt transition, just as discussed here. 

In this paper, Camille Hankel and Eli Tziperman present some interesting results regarding the estimate of tipping-point behaviour in a simplified 1-D sea-ice model, with potential applicability for the analysis of GCM results.

Overall, I enjoyed reading this paper, and think it certainly has great potential for publication in ths journal. In particular, obtaining a method that allows one to more readily estimate and understand the potential hysteresis-behaviour of more complex models would be highly welcome. I think this aim could eventually be reached, but in my view the following overarching points need to be addressed first:

1.  While I enjoyed reading the conceptual framework of estimating potential tipping point behaviour of sea ice, it did not become fully clear to me which part of this analysis is novel also in the broader context of dynamical-system analysis, and which part is primarily an application of known concepts to the case of sea ice. Either cases of novelty would certainly be fine, and welcome, but it'd be helpful to have more information on which part of the paper falls into which category.

2. I am happy to accept the validity of the general framework as outlined here, but I am much less certain that the results obtained here are applicable to the real world. While the authors are careful in not over-emphasising their results in this regard, I think that a broader discussion of the applicability of the Eisenman-model for the analysis of real sea ice seems warranted, in particular in light of the (in my view excellent) study by Wagner and Eisenman, 2015 ( https://doi.org/10.1175/JCLI-D-14-00654.1 ). How do the limitations of the employed model affect the general validity of the results obtained here?

3. I think it'd be very helpful for a geo-physical audience if the distinction between "abrupt changes" and "hysteresis" would be made more explicit. Not all tipping points need to be "abrupt" (depending on the definition of this term) and not all abrupt changes indicate hysteresis behaviour. For example, I would assume that many of the "abrupt changes" in winter sea ice in GCMs as analysed in Bathiany et al., 2016 are fully reversible if the argumentation of their paper is correct. Being clear upfront as to which of these different dynamic behaviours are studied here would help, in particular given that these concepts are sometimes a bit muddled in the literature.

4. Some reference to the common concepts of obtaining effective climate sensitivity in 4x CO2 simulations from curve fitting etc. seems warranted, given that these concepts are at least to some degree similar to the concepts suggested here. (e.g., https://doi.org/10.1029/2003GL018747)

5. Given that this study is framed as a proof of concept for the applicability in GCMs (at least this is what I perceive as the overall framing, for example in the abstract), I think more discussion is needed on the applicability of this idea. For example, which equilibrium states would you suggest for the CO2 increase / decrease runs? How do other ESM-components affect the applicability of this method? Should parts of the ESM be held fixed? Would this method allow one to study equilibrium of all major ESM components that might exhibit tipping point behaviour from the same set of simulations? Is there anything specific about the analysis of sea ice from these simulations?

Some minor additional comments:

l. 2: "Collapse of a sea-ice equilibrium" sounds dramatic, but it is unclear to me what you mean by this terminology

l.11: Also winter sea ice has retreated rapidly in recent decades

l.15: "Abrupt loss or tipping point": These are different concepts, so shouldn't be merged I think

l.54: I wonder if this is a major, robust result of this study that should be highlighted more?

l.138: Should this read Figs. 1a,c,e?

l.147: Duplicate "Li et al"

I hope that you find the above helpful for sharpening the focus of this study. I look forward to hopefully seeing a revised version of this study!