The manuscript reports lidar observations of a persistent smoke aerosol layer in the upper troposphere lower stratosphere (UTLS) in the 7 – 18 km altitude range during Arctic Winter 2019 – 2020, which was characterized by a very strong and long lasting stratospheric polar vortex. The lidar was implemented on the Polarstern icebreaker during the MOSAiC experiment that was dedicated to the observation of atmospheric compounds at very high latitude in the Arctic. The manuscript provides interesting and detailed insights of range resolved aerosols observation in the high Arctic latitude region that is generally subsampled. Observations are of high quality and convincingly described. The manuscript is well written with generally adequate reference to recent work on the subject. However, there are a number of issues and recommendation that need to be considered before publication in ACP.

Major comments

1. In the introduction, the authors mention that the burning season in 2019 was largest on record, they also employ superlatives like “tremendous environmental disaster” without a quantification of how the wildfires compare to previous years.
2. Little information is provided in the article on the Polarstern trajectory with respect to the stratospheric polar vortex. A figure showing potential vorticity and temperature evolution along the cruise is lacking. Such a figure would be very useful for interpretation of the measurements and especially for section 4 that addresses PSC, smoke aerosols and ozone depletion.
3. The fact that the observed aerosol layer originates from the Siberian wildfires is not demonstrated in the manuscript. As mentioned in the paper, several other sources of aerosols can be identified during that winter: volcanic aerosols from the Raikoke eruption, aerosols from pyroCb injection linked to fires in Northern America and PSC. The distinction between smoke and volcanic aerosols is made primarily from the spectral difference of the lidar ratio without consideration of meteorological processes that could further document the origin of the observed aerosol layer. Only one ensemble of trajectories is displayed for one day in the campaign in the manuscript. Such considerations on the evolution of meteorological evolution during the Arctic winter is needed especially in order to better differentiate smoke aerosol from PSCs.
4. The methodology used for the analysis and retrieval of aerosols parameters is not described in sufficient quantitative details. The description relies mainly on references, some of which e.g. Ansmann et al., 2020 is still under review. For instance, section 2 does not summarize the method used for deriving main aerosols parameters such as the backscatter coefficient or the lidar ratio and their respective error. A table could summarize main characteristics of these retrieved parameters in terms of error and vertical resolution. A summary of the POLIPHON method used to derive the aerosol mass concentration is also needed. The GMAO method is used to retrieve the tropopause height but no explanation is given on why such method is better than the classical WMO one. Since tropopause height is generally more difficult to determine at high latitude than at lower ones, such explanation is needed. Also, a description of the method used to derive the bottom and top of the aerosol layer is lacking.
5. The hypothesis of mixing between several particle types is not fully explored. For instance, there is no clear explanation of the quantification of less than 20% for the fraction of volcanic aerosol observed in Fall 2019 (page 7). In Figure 9, PSC are only identified over the smoke aerosol layer. Is there a possibility that PSC are also formed within the aerosol layer? Without knowledge of temperature history, it is difficult to conclude.
6. What is the objective of section 3.3 (comparison with foregoing Aerosol studies)? This section cites a number of other studies analysing aerosol vertical distribution in the Arctic but not clear conclusion is driven from this section.
7. In the same way, the discussion of the interplay between PSC, smoke aerosol and ozone depletion is very vague and relies only on general considerations. The link between PSC formation and persistence, and ozone depletion is quite well known. There is no demonstration that the smoke aerosol layer played a role in the ozone depletion. Qualitative arguments are based only on coincidences in the height range of the aerosol layer and strong ozone depletion. Both section 3.3 and section need to be better focused and reduced in size.

Specific comments

P2 L16 – 19: What parameters were considered from FIRMS and CAMS databases?

P2 L34 – 35: Provide details on the mentioned simulations.

P3 L7 – 9: How do we know that the aerosol was trapped in the strong polar vortex?

P5 L8 – 9: How were identified the PSC: by visual inspection? There is no explanation.

P6 L14: How are the bottom and top of the aerosol layer determined?

P6 L18 – 20: The HYSPLIT trajectories do not demonstrate that the smoke aerosol layer could have been trapped within the polar vortex. Figure 5 is not very clear: provide explanation for the colours of trajectories.

P6 L23 – 24: How are determined error bars in Figure 6? Are they shown as one or 2 sigma?

P8 L28 – 31: How are the refractive index and SSA shown in Table 1 determined?

P9 L22: Figure 10 is not well explained. Significance of the layers mentioned in the legend is not clear.

P9 L23 – 24: If the aerosol layer was trapped in the strong polar vortex, how could it be influenced by smoke aerosol from lower latitudes? What about subsidence within the vortex? The situation of the lidar measurements with respect to the polar vortex is not clear and needs better description.

Ohneiser et al. present a summary of a persistent wildfire smoke aerosol layer observed during the MOSAiC field campaign in the high Arctic. The authors primarily focus on observations obtained from the "Polly" Raman lidar operated onboard the Polarstern, but also compare with other lidar platforms (e.g., CALIPSO and KARL). With the unique observations made possible by Polly and the MOSAiC campaign, the authors are able to provide quantitative descriptions of the optical and microphysical properties of observed aerosols for a region where such measurements are sparse. These measurements are made even more important by the unique atmospheric and aerosol conditions related to the 2019 Siberian wildfires and the unique polar vortex and ozone conditions of late-2019 and early 2020. 

I am not a lidar measurement expert; in fact the editor has asked me to provide my views for portions of the manuscript related to polar vortex conditions and ozone depletion. However, I of course read through the entirety of the paper (multiple times), and so I feel comfortable saying that the paper is generally well-written. While I can not provide an expert assessment of the observational aspects and descriptions, as a "knowledgeable layperson", I'd say The authors mostly gave thorough and convincing descriptions of the observational data and their characterization. The paper is clearly cutting-edge and would be a perfect fit for ACP. However, I do have a few concerns, some more major than others; most of these are related to the aspects surrounding the polar vortex and ozone depletion in Section 4. Since Section 4 is a relatively small portion of the overall paper, I would say the revisions required to address my comments would be relatively minor to implement, but I do feel strongly that they are necessary changes. 

General comments

(1) In reading through the paper, reaching Section 4 felt like a definite shift. Up to that point, everything felt (as a reader) mostly authoritative and backed up by quantitative results. In contrast, Section 4 felt very vague and overall speculative. One paragraph particularly stuck in my mind -- p14, L10-15 -- as it included many instances of language such as "were probably ..." and "were likely". Three "precise" research questions are posed early on in the section, and yet the remaining results and discussion do nothing to answer them and instead involve results that only hint at possibilities. Section 4 essentially says "the smoke aerosol layer could have been important for ozone depletion" simply because the PSC, smoke, and ozone depleted layers overlapped in the vertical (Figures 15 and 16). 

There are many details that would have to be worked out in much more detail to answer the questions posed in Section 4. For instance, if the MOSAiC measurements were to be of use in answering these questions, then there would need to be details about the time-varying geometry of the vortex. While it's a fairly safe assumption that the vast majority of measurements (lidar, ozonesondes, etc) sampled air within the polar vortex, on weekly timescales the vortex and its edge are quite mobile (and similarly, so is the region of air cold enough to form PSCs). This means that measurements could sometimes sample air in different parts of the vortex, meaning some measurements would be less relevant than others in establishing where things were "in the right place at the right time". 

As written, I do not feel Section 4 should be kept.  I would suggest that it should be shortened and perhaps folded into the current Section 5, with content from Section 4 forming the basis of some discussion (i.e., providing motivating context for future work). At the very least, Section 4 should be shortened and rearranged so that the authors present the "possibility" before posing the big picture questions. The authors should also be clear (if they keep any of Figures 15 or 16) that conclusions cannot presently be drawn from their analysis.

In my specific comments below I provide more detailed questions/comments related to the content of Section 4. 

(2) Again, this is not my area of expertise so perhaps these are naive questions: The title of the paper and the introduction generally outline the assumption that the smoke aerosol layer measurements were tied to the Siberian wildfires, but are there not other potential confounding sources? Can the authors provide more evidence to say that the Siberian wildfires were likely the dominant/overwhelming contribution to the observations discussed throughout the paper? The paper lacks some descriptive context as well: how severe were the 2019 Siberian wildfires in comparison to prior years? It is perhaps fortuitous that the MOSAiC campaign was able to sample aerosol conditions largely influenced by Siberian wildfires, but is there a quantitative measure of how unusual 2019 was that would better emphasize the importance of the MOSAiC measurements? These kinds of details may be present in the articles that the authors cite, but I think it's worthwhile for the authors to make them explicit where possible. 

(3) There were a couple of times in the paper where a Figure is introduced and a portion of it is discussed, but then the discussion moves onto one or more different figures before later coming back to the initial one. An example of this is Figure 9: On page 9, line 17 Figure 9a is introduced, but then within the same paragraph the authors move on to Figure 10. The authors go back to Figure 9a, and eventually introduce Figure 11 before eventually mentioning Figure 9b. I recognize that this may just be personal preference, but I think that cases like these generally suggest that text or figures should be re-organized to better maintain the serial nature of the text. 

I understand that in the final manuscript the authors will generally not have much of a say where figures will end up in relation to the text, but it is still a bit awkward for a reader to have to flip between multiple figures for a given piece of text (whether on paper or digitally). I wouldn't classify this as a major issue in this paper, but I still urge the authors to consider whether their figures or text could be restructured to make things flow more naturally. 

Specific Comments

P6, L17 and Figure 5: The information about the arrival height of 10km should be included in the figure. Also, what about the vertical information? How did these trajectories evolve in terms of altitude/pressure over this time period? Is this not important information for discussing the airmass origins?

P10, L22: I do not believe the Lawrence et al ref here shows that the polar vortex collapsed on 20 April. In fact, their Figure 10 shows the vortex was unusally long-lived, lasting into May. Maps of the vortex on April 20 (https://fluid.nccs.nasa.gov/reanalysis/classic_merra2/?one_click=1&tau=00&level=50&field=epv&region=nps&fcst=20200420) show that the vortex was undergoing a split, so it's probably fair to say the vortex began decaying around this time. However, if you click through further dates at the above link, I think it's clear that a distinct polar vortex is present well into May. This comment is also relevant to other spots in the text where the authors mention the vortex collapsed in late April (e.g., P2, L11). 

P13, L14-15: This requires more nuance; it wasn't just weak planetary wave forcing, but also the very strong dynamical influence of downward wave reflection events during the 2019/2020 winter season (this is discussed in detail in the Lawrence et al ref).

P14, L3-9: While questions 2-3 are interesting and are worth further exploration, I'm not sure question 1 has much scientific merit in relation to the polar vortex. There are too many issues with timing and location and other confounding factors. Early in the season, the polar vortex was generally not extremely strong or weak (see https://ozonewatch.gsfc.nasa.gov/meteorology/figures/merra2/wind/u60n_50_2019_merra2.pdf). Furthermore, the very strong vortex conditions in Jan-Mar coincide closely with the dynamical downward wave reflection events mentioned above. 

P14, L18-22: While true, I'm not convinced this is an appropriate apples-to-apples comparison. For instance, the 2019 Australian wildfires were severe enough to be comparable to a moderate volcanic eruption in terms of the impacts to solar radiation (as noted in the Khaykin 2020 paper already cited). I do not think that the Siberian wildfires have been established as being anywhere near as severe. There are other differences, but the point is, this kind of comparison runs the risk of equating inherently different events, which could be much more coincidental than this statement suggests. 

P14, L23: How much of this introductory material is actually necessary for introducing the two figures of the section, which don't actually answer the "big questions" posed beforehand? The beginning of this section sets up big expectations that aren't met. 

Figures 15 & 16: These figures appear to me to be mostly redundant. Figure 16 is mostly a coarse-grained version of Figure 15 with additional information about the ozone anomalies. It seems like this information could easily be combined into a single figure.

P16, L16-22: This paragraph and Section 4 (which has major issues) seems like a missed opprtunity to provide expert guidance on how MOSAiC measurements could assist future studies that may attempt to answer such questions.