Verification of parameterizations for clear sky downwelling longwave irradiance by Pace et al. uses data collected from Thule, Greenland, to evaluate parameterizations for estimating the downwelling longwave flux at the surface based on screen height meteorological measurements. I have not seen an intercomparison quite like this and I think the results are of interest and publishable in AMT. I have a few minor comments for the authors to consider before this manuscript is published.

• A major revision that expands this analysis to include the other YOPP supersites (https://www.polarprediction.net/key-yopp-activities/yoppsitemip/the-yopp-arctic-and-antarctic-supersites/) would make the conclusions more broadly interpretable. However, I respect the scope that the authors are setting and if they do not wish to expand the analysis, I think it would be beneficial to provide some additional text contextualizing the Thule area. For example, northwest Greenland is within a small sub-region of the Arctic where the atmosphere is generally drier (lower IWV) (e.g., Cox et al. 2012) and indeed in the vicinity of 1 cm IWV, there are spectral effects (Cox et al. 2015) that I suspect could impact derivation of coefficients for the parameterizations (more challenging still if one were to interpret Thule data as representative of higher elevations over the ice sheet). Clouds at Eureka, Canada, also in this dry region, are higher, colder, and thinner (e.g., Shupe et al. 2011) compared to much of the rest of the Arctic. Thus, Thule may not be an ideal analogue for either the ice sheet or for the Arctic as a whole. That does not to devalue the results presented here, but is relevant context for readers to understand.
• Long and Turner (2008) is essential reading on the topic presented here and should be referenced and considered for this study as well as future work (as indicated at L432-438).
• Could you explain in more detail (more quantitatively) the accuracy of your clear-sky detection method (L67-69)? Could you clarify if it is necessary to capture all instances of clear-sky or (I think) only to capture a large sample of confidently detected clear-sky? Could you clarify the sensitivity of the vulnerability in this method to assigning “clear-sky” to cases with high, cold, optically-thin (e.g. cirrus) clouds?

Some editorial comments:

• L37: Ohmura et al. (2001) is a good reference here as well.
• Figure 1: I assume the straight lines in 3 & 4 (just before 2018.75) and the bottom panel (between 2017.75 and 2018.00) are artifacts of the plotting technique? Some other short periods in year 2 bottom panel as well. Can these be removed so we can properly visualize data gaps?
• The word “which” is used frequently in places where the correct word is “that” (e.g., L16, 24, 25 but then throughout the text).

References

Cox, C. et al. (2012) A comparison of the atmospheric conditions at Eureka, Canada, and Barrow, Alaska (2006-2008). J. Geophys. Res., 117, D12204, https://doi.org/10.1029/2011JD017164

Cox, C. et al. (2015) Humidity trends imply increased sensitivity to clouds in a warming Arctic. Nat. Comms., 6, 10117, https://doi.org/10.1038/ncomms10117

Long, C. and D. Turner (2008) A method for continuous estimation of clear-sky downwelling longwave flux developed using ARM surface measurements. J. Geophys. Res., 113, D18206, https://doi.org/10.1029/2008JD009936

Ohmura, A. (2001) Physical basis for the temperature-based melt-index method, J. Appl. Meteorol., 40(4), 753 – 761, https://doi.org/10.1175/15200450(2001)040<0753:PBFTTB>2.0.CO;2   

Shupe, M. et al. (2011) Clouds at Arctic atmospheric observatories. Part I: Occurrence and macrophysical properties. J. Appl. Meteorol. Clim., 50, 626-644, https://doi.org/10.1175/2010JAMC2467.1

First of all I would like to sincerely apologize for the delay of my revision.

The paper by Pace et al. investigates the performances of different parameterizations to estimate the clear–sky downward longwave irradiance (DLI) based on comparison against ground–based observations at the high latitude station of THAAO, Greenland. A set of 17 empirical formulations for the DLI are tested. The authors use two full year observations (2017 and 2018) with the aim of: 1/ evaluate original formulas against 2017 data; 2/ use 2017 data to provide optimized coefficients for the THAAO conditions; 3/ test the optimized coefficients against 2018 data. Observations at THAAO used in the present analysis include IBT (infrared zenith sky brightness temperature) and DLI, as obtained from pyrgeometer and pyrometer instruments, and meteorological parameters. The pyrometer data are used to derive cloud–free periods based on an original algorithm, while the pyrgeometer data are used as direct comparison against calculated DLI with the 17 different formulations.

The paper is well written, clear and logically organized. The dataset, the procedure, the figures, and the results are clearly presented and discussed. The final scope of this work, that is providing optimized estimates of the clear–sky DLI to use then in future works to estimate the cloud direct radiative effect in the infrared spectrum at THAAO, is clearly identified and of potential interest also for other researcher. The work fits within the scope of AMT and publication can be suitable after minor revisions. I propose here some suggestions to potentially clarify some aspects and broad the conclusions, as well as some minor technical remarks.

Abstract, line 20: “The bias displays a significant improvement when the coefficients of the different formulas are calculated using the THAAO dataset.” This is somehow obvious, I guess. I would suggest:  ”As expected, the bias displays a significant improvement when the coefficients of the different formulas are calculated using the THAAO dataset.”

Abstract, line 21–22: “The presence of two full years of data allows the investigation of the inter–annual variability,”. I am not sure that two years of data are sufficient for performing an analysis of the inter–annual variability. On the contrary, as discussed in Sect. 4.1, the two years are interesting to be used in this study since they show different conditions to be tested. I would put this aspect in evidence in the abstract.

Introduction, lines 28–29: references would be good at the end of this first sentence

Introduction, line 40 and wherever this applies: very minor comment, but when possible it is better avoiding to start sentences with acronyms

Introduction, lines 40–42: references would be good at the end of this sentence

Section 3: Two comments here: 1/ it would be useful to show (even in the supplementary) a plot illustrating the distribution of clear–sky periods during the two years under consideration. Somehow the discussion of the results in terms of seasonality is missing and it would be good to start from the identification of the distribution of clear sky periods. 2/ I understand this cloud–screening procedure is somewhat original. If this is correct, would not be worth to put this more in evidence in the paper? This could imply a few changes in the title/abstract/general discussion. I let the authors to evaluate if this is pertinent or not.

Section 6, general comment: the analysis of the seasonal dependence of the performances of the different formulas is not provided. Have the authors’ analysed possible seasonal changes in the performances of the different formulas both for original and the THAAO–optimized formulations? Can they provide some insight on this aspect or derive useful information from this analysis? In some points the discussion the authors mention that original formulations derived based on partial year data are not good because of this limited time period used as reference. In order to better understand this point, it would be appropriate to discuss the seasonal coverage of clear–sky data used for THAAO analysis (see previous comment) and the seasonal changes (if there are) of the performances of the different formulas.

Section 6.2: can more details be provided on the procedure to estimate the optimized coefficients?

Section 7, lines 400–401, I would skip those two lines, it is a repetition

Section 7, line 408: see my previous comment on the “inter–annual variability”

Section 7, line 432: worth to point out that the 5–7 Wm^–2 is within the uncertainty of the DLI by pyrgeometer, as discussed earlier in the paper

Section 7, general comments: based on the analysis and conclusions of the paper, two points can be raised and maybe deserve a word of conclusion from the authors. Firstly, as at the end the DLI parameterizations are site–dependent, one may ask if, for a specific site, the tuned–parameters derived for a specific year can be used to predict the DLI no matter which year of application or not. In other words, a discussion about which statistics/time range can be reasonable to consider for proper use of tuned–parameterizations should be added. Secondly, does the authors have any hypothesis on why the DLI parameterizations are site–dependent or which parameters seems to affect the most the formulation? Any conclusion or direction to provide generalization of the results would be for sure very much appreciated by the community. In particular, to what extent the tuned parameters for a site (THAAO for example) can be of relevance for other sites or not can be discussed by the authors.