The authors combine CMIP6 model output with reanalysis data, observations and LES model results to investigate the inter-model spread in Arctic amplification (AA) and the Arctic lapse-rate feedback (ALRF). When sorting models into models with stronger and weaker AA and ALRF, strong AA/LRF models better match reanalysis trends in heat advection, whereas weak AA/ALRF better match observed present-day inversion strength.

The presented data and work is interesting and relevant to important research questions, but I have a few major concerns on how the model-observation analysis is carried out:

1. The authors do not investigate the role of internal variability for model results
   
   Investigating only one ensemble member per model without regard for the ensemble spread might not do justice to models – even a clear mismatch with observations does not rule out that the model in question is consistent with the observed trend or phenomenon (see eg Notz 2015).
2. Important conclusions rely on small subsets of the analysed models, comparing only the top and bottom three models in terms of AA/ALRF. For the weak AA group, these are clear outliers in the CMIP ensemble, and two of the three are different versions of the same model. Would the results remain the same (just with weaker signals) if models 4-8/24-28 were used instead?
3. The definition of AA as a difference dT_Arctic -dT_global rather than a ratio dT_Arctic/dT_global is surprising to me. Wouldn’t one expect most mechanisms driving AA to act in a multiplicative rather than additive way? Similarly, the choice of the reference period is unclear to me. If no observations from the reference period are used, why not choose an earlier reference period (PI or at least 1850-1880 historical) to maximize the signal?

Minor comments:

ll 22 ff and elsewhere in the manuscript: Now that the work is done, I feel that the manuscript would be stronger by focusing on what has been achieved rather than what the authors want to achieve.

l. 65 ff: The impact of clouds on the vertical temperature profile has not been introduced at this point in the manuscript.

l 205: showing that 2019/2020 is equivalent to 2009-2014 using scenario output would be stronger than just assuming it – strong changes have happened in the Arctic in the early 21^st century.

For the comparison with radiosondes, I would recommend coarsegraining the radiosonde profiles to the vertical resolution of the models at least as a sensitivity test (same for NSA).

Section 2.4: Comparing March/April measurements with DJFM model data – did you check that model data looks similar for March as for the entire winter season? Do we expect the 1993 campaign to show the same climate state as the 2019 campaign?

l 385: do all models have similar inversion strengths in the reference period?

l 407: what is the timeframe covered by the Kahl (1990) study? Do we expect it to be representative of 2020 conditions?

l 487: what significance level? How did you do the bootstrap analysis?

Fig. 10 and related analysis: This shows data year-round, is there a relevant seasonal cycle?

l. 564: Cronin and Jansen (2016) would be a good reference here

l.  585-590: I think this is an important result deserving a stronger emphasis in the paper, since entrainment has not received a lot of attention in this context so far.

l. 592 “we compile a sizeable amount of observations” Here and elsewhere in the paper: There is nothing to be said against impressing the reader with the large array of observations you bring to the task in addition to CMIP and LES data, but in my view this works better if you leave being impressed to the reader.

l. 687: I think a crucial point here is that CMIP6/s models generate less warming for a given amount of sea-ice retreat. If this is correct, it should be stated more explicitly.

Cronin, T. W., & Jansen, M. F. (2016). Analytic radiative‐advective equilibrium as a model for high‐latitude climate. Geophysical Research Letters, 43(1), 449-457.

Notz, D. (2015). How well must climate models agree with observations?. Philosophical Transactions of the Royal Society A: Mathematical, Physical and Engineering Sciences, 373(2052), 20140164.

This paper aims to dissect the Arctic warming simulated in the CMIP6 models by comparing them to observations. The analysis is centered on the geophysical variables related to the lapse rate feedback, which, as argued by a number of studies, is of critical importance for the Arctic warming amplification. To the extent this argument is valid, the comparisons in this paper are well motivated. A novel aspect of this paper is that it includes comparisons to several different kinds of data, some of which, such as the newly acquired Mosaic campaign data, provides fresh perspectives for model validation. However, although each comparison included here potentially provides a useful line of evidence for discriminating the models, unfortunately few results appear conclusive in the end. This calls into question whether one had better aim to identify and focus on what can be more conclusively stated about the models and/or nature, as opposed to a somewhat nonselective listing of results. Moreover, the use of some data and analysis methods are not sufficiently explained (see comments below), raising questions about their properness. For these reasons, I think the paper would need a major revision before being considered for publication.

Figure 1. Can you also provide the observations for a comparison in these diagnostics?

L172 "consistency": can you provide any reference to this belief? Note that it is quite known that there are noticeable differences between different kernels, especially in the Arctic. In either case, it would be move convincing to provide an error bar based on results computed from more than one kernel.

L205, 251 use of years of 2010-2014. Can you justify the use of these model years to match the observation? It's understood coupled model years are nominal but what guarantees a comparison done here, between a single realization of nature of limited length and multiple model years, is proper? Very handwavy to "assume" they're "roughly the same".

L261 The identification of different "regimes" looks an interesting approach to me. However, I found the description of the method too brief here. I'd suggest showing the relevant results such as the EOFs, as well as the associated PCs and eigenvalues. I think this method, like the other data and methods in this paper, is worth more careful/critical reasoning and more thorough discussion.

L290 What's the basis of using this proxy as a quantitative measure of the energy transport? How can the TOA-only perspective differentiate atmospheric vs. oceanic transports? How is equilibrium verified, so that horizontal transport can be inferred from vertical energy flux?

L305 and Figure 9, concerning the use of satellite OLR records, it should be noted that various issues had been documented on how wrong it could be to take a non-SI-traceable radiation record as the ground-truth of "observed" long-term trends. For example:

Trishchenko et al. https://doi.org/10.1029/2002JD002353

Wong et al. https://doi.org/10.1175/JCLI3838.1

The OLR trending itself would be worth a full section if not a paper by itself. Before its correctness is established, it is very questionable to use this result as a model discrimination metric.  

L380 "significant". Although significant differences are stated here and at multiple other places (in this (Figure 4) and other figures), looking through these results, I am not convinced there is indeed any strong difference between the compared groups, either between "w" vs "s" or between them and the observation (Mosaic). If the discriminations are based on such weak evidence, I am not sure the observation used here provides any useful constraint as wished by the authors, or any model evaluation result can be considered conclusive. Please critically review and reason about this and other conclusions.