the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 26 May 2026
What surface radiative fluxes reveal about Arctic cloud modelling accuracy
Abstract. Low-level clouds exert a strong control on the Arctic surface energy budget, yet their representation in regional atmospheric models remains a major source of uncertainty. We evaluate the Weather Research and Forecasting (WRF) model against observations from the Norwegian Young Sea Ice Experiment (N-ICE2015), conducted north of Svalbard from polar night to polar day. The analysis focuses on downward surface shortwave (SW↓) and longwave (LW↓) radiation under synchronous cloudy conditions to diagnose cloud-related radiative biases. While near-surface meteorology is generally well reproduced, pronounced seasonal radiative errors emerge. A dominance analysis based on a simplifed two-layer emission framework shows cloud emissivity, primarily controlled by liquid water path (LWP), is the leading contributor to LW↓ errors. During spring transition, the model underestimates cloud occurrence and simulates optically too thin clouds, leading to excessive SW transmission and insuffcient LW trapping. During polar day, a marked negative SW↓ bias develops. Radiative errors are largest for LWP below 30–40 g.m-2, where cloud optical properties are highly sensitive to variations in liquid water content. Sensitivity experiments demonstrate that improved representations of sea ice cover and surface albedo reduce polar day SW↓ biases, while modifying prescribed cloud droplet number concentration alters optical thickness but introduces compensating errors. Clouds diagnosed as surface-decoupled exhibit lower LWP and larger radiative biases, and this regime is overrepresented in the model. These results highlight the need for consistent representation of surface properties, boundary-layer structure and mixed-phase microphysics to improve simulations of Arctic surface radiation.
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Status: final response (author comments only)
- RC1: 'Comment on egusphere-2026-2516', Anonymous Referee #1, 27 Jun 2026
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RC2: 'Comment on egusphere-2026-2516', Anonymous Referee #2, 08 Jul 2026
This paper addressed surface radiative fluxes over the Arctic and uses observations from the N-ICE2015 campaign to evaluate WRF model simulations and diagnose the causes of model radiation biases. The topic is an important one as cloud-radiation-system interactions are one of the factors that influence Arctic climate, they continue to pose challenges for models, and there is a need to extract whatever information is possible from the limited existing observations. In these regards, the paper is an important contribution and is thematically within the scope of ACP. However, this manuscript has several major shortcomings that lead me to question its fundamental findings. Many employed methods have unquantified and undiscussed uncertainties and could be readily replaced with more consistent methods or more reliable data. Thus, while the manuscript’s goal of explaining the specific contributions to model bias is a good one, and some of the results could provide useful insight, I do not believe those results should even be considered until the major methodological deficiencies are resolved and the analysis can be re-done. This will require significant additional work in most parts of the study. At a minimum, this would be a case of “Major Revisions.” Specific comments are included below, distinguished into some of the major methodological issues and then more general comments.
Major Methodological Issues
Line 162: Why does the threshold change so much between the different periods of observations? During MOSAiC, Shupe et al. (2026) applied this same LWN threshold approach but found that -25 W/m2 worked for all seasons. Why the difference here? Is there a physical explanation or something markedly different about the atmospheric scenes in this part of the Arctic during winter? Also, these different definitions will make the different periods incomparable with each other and hard to interpret. I believe this difference manifests itself into some of the results presented later in the analysis, but its role is not discussed.
Line 176-181: As described in this paragraph, it is apparent that the cloud conditions are identified using LWN in the observations but CLT in the model. The reasoning presented for why this difference is implemented is the role of spatial variability in cloudiness that could impact the radiation measurements. That is a valid concern, however, the observational dataset does not have information on spatial distribution of cloudiness. That is an unavoidable limitation of these observations. But given the observations, it makes more sense to at least apply consistent definitions. Why not just apply the same LWN threshold approach to both observations and models so the different definition does not add further, unquantified, uncertainty to the comparison? The comparisons that are shown later clearly reveal some influence from this difference in definition, but that influence is not discussed nor quantified. Moreover, it really doesn’t make sense. “Clouds” have many definitions. Thus, to have any hope of legitimately assessing a model, it is important to at least define them in the same way between observations and models.
Line 201-205: It is a bit strange that the model shows a lot of low LWD values that are not observed. I believe this figure has only the cloudy sky subset of data described in the previous section (although that is not entirely clear). If so, these low simulated LWD values would have to come from clouds that are vastly thinner and/or colder than those that were observed. This signature would be consistent with a discrepancy in the definition of clouds. Since the observations are simply based on LWN threshold, they will all have a high LWD. Since the model results are based on this CLT, there is no guarantee they will have high LWD. In fact, based on later parts of this manuscript, it appears that “clouds” are also defined where there is ice/snow via the modeled ISWC. Thus, if I had to speculate, I would say that these low LWD values are from times when there is only ice/snow in the model with little to no liquid water. This is a demonstration of the apples-and-oranges comparison that results from the different cloud definitions.
Line 214-238. There are a lot of problems with this general approach to assessing the clouds and radiation, as outlined in the following six points:
1) Eq 1 includes some of the terms that contribute to LWD and is mostly correct when Ec is approaches 1. When Ec is significantly less than 1 this means there will be contributions from the atmosphere above the cloud (possibly from multi-layer clouds that are at a different temperature), which are not included here. This point is kind of mentioned at the end of the paragraph but is not included in the equation. Overall, this equation is approximately true only when Ec is high.
2) Having "almost all" cloud base heights less than 90m would be a remarkable result for observations over nearly 5 months extending from winter to early summer. It is divergent from other observations, including those from MOSAiC. I do not believe this statement is true. I have tried to assess the results of the Maillard et al. (2021) paper, but there is no actual lidar data shown with which to independently verify that the lidar really identified almost every cloud base to be below 90m. Thus, without further information, my interpretation of this result is that the “cloud base” referred to here is actually the base of “hydrometeors”, including falling ice. In that case, yes, the base of hydrometeors would most commonly be near or at the surface because there is quite often falling precipitation. However, this base is not always (or not often) the base that is important for radiation. I believe N-ICE had a ceilometer; why not use actual cloud base height measurements from a widely trusted system like that? Ceilometer reported cloud base would be more consistent with the radiatively-important cloud base.
3) Building further on cloud base: In the description of the model analysis, it is stated that cloud base is defined when LWC exceeds 10^-5 kg/kg or when ice/snow exceeds 10^-6 kg/kg. As outlined in the Introduction, ice and snow have vastly different interactions with atmospheric radiation (for a given amount of mass) due to microphysical properties. By defining things in this way, you will get artificially low cloud base heights under all-ice and mixed-phase conditions that will be identified based on weak ice/snow precipitation, which has a low total emissivity. Thus, it is not a good approximation of the location where most emission occurs. i.e., the assumed cloud emission temperature will be wrong. This incorrect identification of cloud base could be part of the reason you identify most modeled cloud bases to occur in the first model level, but I do not have enough information to know for sure.
4) On a related topic: The assumption that cloud base temperature and surface temperature are equal is highly uncertain, condition dependent, and effectively forces the implied LWN to be 0 W/m2 under thick clouds. In reality, there is usually a negative temperature lapse rate over some layer below cloud base (i.e., usually adiabatic ascent helps to form the cloud), which could overlie a variety of temperature structures at lower levels. In the best-case scenario (for the assumption made here) with a low, surface-coupled cloud the temperature difference might only be a couple tenths of a degree. However, for real cloud bases that will often be significantly >100 m above the surface, the difference becomes important. We already know that Eo is small and in the limit where Eo approaches 0, Eq 2 becomes simply LWD=Ec*sigma*T2m^4! This is a poor approximation.
5) The analysis uses Eq 1 for model data and Eq 2 for observational data. How then can the results be compared to each other? The method alone will have a large uncertainty that could mask other issues in the model. To truly evaluate the model, you must apply the same approaches to both observations and model results.
6) Simply throwing out cases with Ec > 1 is not a sufficient remedy for the shortcomings of this approach. In general, I would expect the smallest uncertainties to occur when Ec is highest (i.e, that is when Eq 1 is most accurate). Ec values > 1 do indeed indicate a bias, but it could be a smaller bias than cases with lower Ec values (which are retained in the analysis). The main point here is that the whole analysis is highly uncertain because the equations and assumptions used are suspect. The impact of these uncertainties has not been evaluated or discussed thoroughly. As a result, I have little confidence in all the downstream results that are presented.
Overall, because of all these points, I do not see how this approach can legitimately be used as presented here.
Line 239-242: I do not understand what information is being shown by this analysis. First, while the analysis examines the errors (LWD model-obs), it does a dominance analysis using Eo, T2m, Tcb, and Ec. I assume those parameters are from the model? Second, Ec was derived from T2m, Tcb, and LWD for the model results (Eq 1). Thus, the respective Ec values are directly dependent on the other parameters. Their contributions to LWD variability are pre-determined by the relationship through which they were derived, not based on independent physical variations. Thus, it is not clear to me how this analysis reveals information about the physics of Ec. Lastly, the assumption that T2m=Tcb (in the observational analysis) is undercut by the different results for T2m and Tcb. These temperatures apparently do not vary the same nor impart the same influence on LWD. If true, the assumption that T2m and Tcb equal each other in Eq 2 neglects some important physics.
Line 272: This point might indeed explain the results in Figure 5 for this dataset. However, based on LWP observations from MOSAiC it was found that the opaque cloudy state (i.e., LWN > -25W/m2) contained a lot of LWP values that were less than 30 g/m2 (see Dahlke et al. 2025, Shupe et al. 2026). Moreover, the fact that a LWN threshold of -10 W/m2 is used in P1 instead of -25 W/m2 means that the “clouds” identified in that period would naturally have higher LWP than the other periods (in a season that routinely has lower LWP and has lower background moisture such that the radiative effects of thin clouds are accentuated relative to the moist summer). First, I do not think there should be different LWN thresholds applied to the different periods. But if there are, the impact of this difference should certainly be discussed thoroughly.
Line 380-383: I have concerns about the accuracy of the “observed” coupling state results as they are based on a fixed cloud base height of 100m that may or may not be correct for any given case. The effect of this assumption on the results has not been discussed. Moreover, with a radiosonding dataset (and only 55 soundings) it should be readily possible to perform a robust determination of coupling state for the available cases. In soundings it is easy to identify a liquid saturated layer (typically a threshold of ~96% RH is used). Then, you can determine the equivalent potential temperature at the base of that cloud layer and the surface. Their difference gives you a clear delineation of the coupling state. This approach is far preferable to making an uncertain assumption about cloud base height.
General Comments
Full text: There are many issues with the written text in terms of grammar, sentence structure, and other issues. While I started noting these in my review, there are so many that I will not include them here. Before proceeding, this manuscript needs a full editorial review.
Line 21: “positive effect” on what? They have a net warming effect on the surface or a positive effect on the surface radiative balance. That should be clarified.
Line 22-23: This statement about “short period of surface cooling in summer” is true over highly reflective surfaces like sea ice. Over less reflective surfaces like land (after snow melt) or open ocean, the cooling period extends for multiple months. This cannot be considered “short.”
Line 24: Cloud radiative parameters are important of course. But this statement is more accurate as “Cloud radiative properties along with relevant properties of the surface and atmosphere……” Ultimately the surface albedo plays a substantial role in the net effect of clouds seasonally that can overwhelm cloud radiative properties.
Line 81: Having only 1-moment liquid leaves substantial deficiencies in representing the liquid phase, as has been shown in prior studies. This is particularly true when you are attempting to examine the effect of, for example, aerosol indirect effects where the second piece of information about the liquid droplet size distribution can be quite important.
Line 116: The model had a rather large warm bias during 14-16 March. What is the cause of this and does it provide any insight into the model issues?
Line 118-120: Importantly, this good agreement during P3 should not be surprising since the surface is melting at the time.
Line 121-126: Since RH is influenced by both the amount of moisture and the temperature, it is better to examine specific humidity to allow for the moisture and temperature to be evaluated separately. It is not clear here how much the temperature biases impact the RH compared to specific humidity biases.
Line 125-126: True, the near-surface RH biases might impact the representation of low clouds under circumstances when the cloud layer is coupled to the surface. However, under decoupled conditions this is likely not the case. Additionally, even for coupled cases, a bias at the surface may not manifest in the same way at the cloud level because of temperature effects. I would be more comfortable with this statement if it were based on specific humidity and with the qualifier about coupling state.
Line 128-129: The point of the paper is to understand the model representation of clouds and their impacts on surface radiation. Thus, it seems important to examine higher resolution data since clouds vary on sub-daily timescales. Daily averages could mask competing / compensating biases. Why not use the higher resolution data in the analysis?
Line 146-148: I do not understand this feedback. If the near surface air temperature is too cold, with all else unchanged (i.e., the overlying atmospheric temperature and the amount of turbulent mixing), the near-surface temperature structure would become more stable, which would diminish upward sensible heat flux (or increase downward sensible heat flux). This then effectively works against the cold bias rather than reinforcing it. Perhaps I’m missing something to this argument, so that should be spelled out more clearly.
Line 172-173: Something is wrong with this sentence. It is only true if “exceeding” means a greater negative value than -25 W/m2, which is not really the correct use of exceeding. Additionally, the clear sky mode (values that are more negative than -25) is not discussed until the next sentence. Thus, maybe here you mean “underestimated”?
Line 174-175: “better representation of the cloudy mode frequency”. Strictly speaking the representation of that mode is better than for P2. However, it is still not good and I do not think the distributions “agree well.”
Line 181: I think this appendix B and Table B1 should be in the main text. The cloud occurrence information is important for the main paper and the reader should not have to search for it at the back of the paper.
Line 193-194: I do not agree with this statement. There are quite different clouds identified using the different approaches and it is not clear how these two datasets do overlap or should overlap with each other. For example, the fact that the observations and model show “quite similar cloud occurrence frequencies” during P3 could be for vastly different reasons due to the different methods for identifying clouds. Even the “synchronous cloudy set” discussed in the following sentence is not very satisfying because clouds that exist in that set could be there for different reasons. Simply use the same method for identifying clouds to eliminate that inconsistency and uncertainty.
Line 198: is this section presenting only results for cloudy periods identified in the previous section? That is not clearly stated in the text, but the caption of the figure seems to indicate so.
Line 199: “retrieved” is the wrong word here. Maybe “simulated”
Line 200: This last part of the sentence is unclear. I believe you mean that the emission of these warm and opaque clouds is underestimated. Correct?
Line 201: Instead of “magnitude” it is better to say “fractional occurrence”
Line 230: Ec is used in the equations while Ecloud is used in the text. Make consistent.
Table 2: The concept of the information presented in this table is very compelling. However, the vast uncertainties in the method, and lack of discussion of how those uncertainties impact the results, leaves me with a notion that these values cannot be trusted. I would need discussion of the role played by interdependence of Ec on other parameters, on the removal of all cases when derived Ec >1, on the identification of cloud base height, on the identification of cloudiness in general, etc. etc.
Table 3 and associated discussion: These are the statistics that go with the distributions discussed in Section 3.2.2 and Figure 4. Why not include this information together in the description of results? Certainly the distributions provide useful information for interpreting the biases and statistics given here.
Line 275: What is liquid water fraction? This has not been defined as far as I recall. Also, just because the LWF ~ 1 does not mean that model phase partitioning is not an issue. Phase partitioning impacts the properties of the liquid and its radiative effects in non-linear ways.
Line 299-300: One important bias that is not stated directly here but is important to highlight is the fact that the observations are at a specific location on solid ice (representing ~10 m^2) while the model grid size is 15x15 km^2. The observed surface will be on the high end of the albedo distribution within a model grid cell, which also includes non-level ice, leads, etc. There has been some work to evaluate such spatial differences when, for example, comparing surface point sources of albedo to albedo derived from satellites with a large spatial footprint.
Section 3.3.4: In this section we have learned that the model can represent the basic first and second indirect effects of aerosols. However, the argument is made that the baseline CDNC is correct. Thus…. Is the conclusion that errors in CDNC are NOT the cause of radiation errors?
Line 359-360: Does this mean that you do not also use the ISWC threshold that was described in Section 3.3.1?
Line 363: How is ABL height defined here?
Line 384-386: This has not been shown. However, it could be shown by making direct comparisons of the model results to the measured radiosonde profiles. Rather than speculate using an indirect approach with uncertain assumptions, it is better to just use the direct measurements that are available.
Line 402: By “clouds are too often underrepresented” do you mean that the model does not produce clouds as often as they are observed? Please clarify.
Line 409-410: Yes, but phase partitioning can impact the properties of the liquid component, which dominates the radiative signal.
Section 4: There is a marked increase in typographical and grammar errors in this final section. I re-iterate the need for a full editorial review of the manuscript.
Citation: https://doi.org/10.5194/egusphere-2026-2516-RC2
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Please see my full referee comment in the file attached.