The manuscript presents a review of the current advances in modeling D-O events with IPCC-class climate models and proposes a common protocol for modeling D-O type oscillations within the PMIP4 framework. While the authors present a comprehensive summary of model simulations that exhibit D-O type oscillations, the respective boundary conditions and the underlying mechanisms they also highlight the limitations of modeling such abrupt climate events with IPCC-class models.

The manuscript nicely summarizes previous simulations of D-O events and allows for a comprehensive insight in the advances and limitations of modeling such abrupt climate events. The authors pose many relevant questions, which, to this point, cannot be answered with great certainty. I believe that the proposed protocol for modeling and better understanding D-O oscillations is valuable to the wider scientific community and for a better understanding of the ability of climate models to simulate past and future abrupt climate events. However, I would like to propose to include some of the limitations of the planned intercomparison study and what we can learn from such an intercomparison in case D-O events do not occur under the proposed boundary conditions (except that the models are too stable).

Specific comments:

The variety of model setups and boundary conditions to simulate D-O-type oscillations that is presented in this study (e.g. Table A1) shows that each model has likely a very different threshold at which D-O events might occur. Hence, the models simulate D-O oscillations under very different ice-sheet states, utilized parameterizations and/or trace-gas concentrations. Proposing a common value for the trace-gases and two different ice sheet reconstructions will help to identify whether the models are capable of simulating D-O events under ‘realistic’ conditions. However, some models might have their threshold at conditions that are close but not within the proposed boundary conditions of the protocol. How to deal with experiments that might formally be outside of the bounds of the experimental protocol but show DO-type oscillations. We likely can still learn something about the mechanisms behind these changes. Hence, I would suggest one additional experiment alongside MIS3-cnt that allows for departures from the protocol (e.g. in terms of atmospheric trace gases – maybe a CO2_variant). Given the mentioned previous studies I doubt that any model will show oscillations at the exact same values that are proposed.

Following the previous point, I am wondering what the authors can learn from the simulations in case the majority of the models (if not all) do not show D-O oscillations under the given parameter ranges. Are there still questions that might be answered. This might add not only scientific credibility to this study but also a motivation for the modeling groups to conduct such experiments.

Abstract: The mechanisms behind D-O events varies between models, as presented in Section 2 and Table A1. In the abstract you only state the question: are our climate models too stable to simulate D-O events? I think the model intercomparison will likely be able to answer more than just this question, hence, I would try to include a little more information on how such an intercomparison study may help to improve our process understanding and/or past and future abrupt changes.

Line 60: In fact, so far you have only posed one question (see comment above). It might make sense to shortly summarize the key questions here.  

Table 1: I liked this short summary of the key terms used within the paper. I was just wondering what you mean by ‘A further issue arises…’ under the term Heinrich stadial. Could you please elaborate in what sense it is an issue whether the H-event stems from the Laurentide or Fennoscandian ice sheet.

Section 2.2: A sensitivity to the ice sheet height is evident in all model simulations presented in the present study. In the protocol two different ice-sheet reconstructions are proposed as boundary condition and Fig. 7 shows that the reconstructions are quite different, specifically in terms of the extent and height of the Laurentide ice sheet. I assume that the modelers can choose between either one of the reconstructions. It would be good to add a small discussion on the uncertainties and differences that are expected to arise in the model ensemble in terms of these uncertainties in the ice sheet reconstructions. Previous studies for glacial-interglacial conditions have shown, that a different height and extent of the Laurentide ice sheet has a significant effect on the AMOC (e.g. Löfverström et al., 2014 - https://doi.org/10.5194/cp-10-1453-2014 or Kapsch et al., 2022 - https://doi.org/10.1029/2021GL096767).

Technical corrections:

Line 75: ‘which do not show these’ – ‘n’ removed, also might be good to refer to ‘oscillations’ instead of ‘these’

Line 77: ‘A number …’ – this sentence is a little confusing and becomes only clear after reading Table A1. Please revise.

Line 161: ‘the sub polar gyre contracts, an inflow of’

Table 1: Bond cycle: ‘following H-events H5 and H6‘ – hyphen missing

Table A1-A3: There are several small typos throughout the three tables, please revise. E.g. Drijfhout et al.: ‘spontaneous cold event that last around 100 years’ – missing s, but there are several more. Also the format is not optimal in some places, specifically when there are several simulations per study.

Review Malmerica-Vallet et al., 2022. COPD.

General comments

This manuscript seeks to do three things: 1. Define nomenclature surrounding Dansgaard-Oeschger (DO) events; 2) Summarize existing model studies, which attempt to model MIS3 climate and/or replicate DO events; 3) Propose a set of protocols for future model studies (via CMIP/PMIP) of MIS3 climate and a so-called “kicked Heinrich meltwater experiment”.

In terms of points (2) and (3) this study should prove a useful addition to the literature. I did wonder if Geoscientific Model Development might be a better home for it though, alongside other CMIP/PMIP protocol papers. Overall, I am supportive of the proposed modelling effort – it is long-overdue and will undoubtedly help to shed light on processes involved in millennial climate change during MIS3 (and is a great improvement on the approach of just using LGM conditions, given that we know from the data these are not conducive to DO events). However, the manuscript itself needs some substantial work before publication.

Specific comments:

• Unclear aim or focus of proposed experiments

The abstract states: “The climate modelling community up to now has not been able to answer the question: Are our climate models too stable to simulate D-O events?” and this appears to be the central question driving this study. Surely we are interested in much more than this binary question? Some might argue we already know the answer – yes, some models are too stable – the important questions are WHY this is, what are the processes that contribute to relative levels of model stability? I suggest that the scientific motivation behind this proposed model intercomparison protocol is explicitly laid-out and justified by the data available. For example at Line 60 “The design of a common MIS3 experimental protocol would allow the modelling community to address the questions posed above” – I have a hard time working out what the questions above are. I note that some questions are introduced later at Line 78.

• Conflation of model and data

Related to the above, the logic of this manuscript is quite difficult to follow because from the abstract onwards knowledge of DO events from primary data (e.g., ice cores, marine sediments) is conflated with model simulations. It is not clear if the project’s motivation is grounded in the data or in model nuances (that may of course be relevant). For example, Line 104-5 states that D-O type behavior shouldn’t be seen under full glacial conditions because it isn’t present in the data – surely that information should be upfront, included as a primary pillar of your protocol design, not mentioned because some models might agree with it?  In Section 2.1, please make clear with D-O type oscillations are in models…in which parameters? What timescale and amplitude satisfies your definition? [n.b., Table 1 states “It is not clear that series of D-O events are oscillations in the strict sense.”]

• Nomenclature

Table 1 is not a useful addition to the literature as it stands. It is littered with errors (too many for me to highlight every one) and introduces further ambiguity and confusion. The ambition to reset nomenclature usage across the entire palaeoclimate community is a large one. It would better to state that you wish to define nomenclature for use within this proposed PMIP protocol and associated papers only.

In table 1: “stadial-interstadial” – these occur in many other time periods in addition to MIS3. Might be worth referencing the INTIMATE naming system here.

“Heinrich events” – entirely inaccurate definition. There is little, if any, evidence to support your claim that Heinrich events “have a role in DO oscillations”. There are small methane peaks within some (but not all) Heinrich stadials that have been linked to Heinrich events. They typically occur mid-stadial not “before a stadial has begun”.

“Heinrich Stadial” This term denotes a Greenland Stadial in which a Heinrich event is thought to occur. A stadial can therefore be both a HS and a GS. Sentence about H event provenance is out of place here!

“Bond cycle” is the term/concept useful or relevant here?

• Heinrich “kick”

Line 68: “In addition to the protocol for a baseline simulation, we also outline a protocol for a Heinrich event (Bond cycle event one type; Table 1) preconditioned variant.” This statement makes no sense to me and Table 1 does not help. Scanning down to section 3.3…the term “kicked Heinrich event” is still not explained. This section needs dedicated attention from co-authors. Stocker and Johnsen 2003 do not discuss “The freshwater delivered during Heinrich event iceberg discharge extends GS duration and suppresses the AMOC”. Why is it “logical to presume that these freshwater events are important in preconditioning the climate system with respect to D-O behaviour”. There seems to be an equally strong argument which states DO events would continue to occur without Heinrich events.

Could the authors clarify what they are trying to achieve or test with this “kicked H-event”? How will they distinguish freshwater flux related to a Heinrich event (iceberg discharge from Laurentide) with other ice sheet instability delivering IRD and [potentially] contributing to AMOC variations that occurred within every DO cycle, H event or not.

• Sections 2.1 and 2.2 contain interesting discussion of the likely processes and feedback involved in generating D-O like events, and the associated figures are well-presented. Throughout though, it needs to be clear how the new protocol will address key questions related to the role of sea ice etc. that the discussion identifies.
• Atmospheric gases

Could you comment further on choice to keep atmospheric CO2 constant? (section 3.1) What does that assume about the role of CO2 in D-O behavior?

Technical corrections

Line 62: “Given…” This is a phrase not a sentence.