Interactive reviewer comment on the manuscript Comparative Evaluation of Boundary Layer Height Estimation

Using Multi-Source Observations and WRF Simulations under

Complex Topography

GMD-2025-427

By Zhong et al.

General considerations

In this contribution the authors use one (or possibly two?) days of observations (Doppler wind lidar, MWR, radio soundings) to compare 6 different BLH schemes in WRF in their ability to diagnose the boundary layer height in truly complex terrain. While this is a (very) timely and important research question they address, I think i) this study does not comply with the scope of AMT (major comment 1), ii) the data available is simply not sufficient to draw any robust conclusions (major comment 2), iii) the topic is not properly addressed (major comment 3) and iv) the paper contains a number of errors and editorial weaknesses (see some of the additional major and the many ‘detailed comments). In this sense, I cannot recommend publication in AMT (I don’t even think that major changes could do the job).

Major comments

• 1) The scope of AMT is ‘…the development, intercomparison, and validation of measurement instruments and techniques of data processing and information retrieval for gases, aerosols, and clouds …. (website)’. The present paper addresses one of these targets (intercomparison) at most, but the focus is on the assessment of the WRF ABL schemes. The few occasions to discuss observational differences (e.g., Fig. 5 → l. 269…), however, are even wasted away: ‘The red dashed line denotes the profile derived from MWR, which exhibits poorer vertical consistency compared to other results and is thus used here primarily as a reference’ (whatever this should mean: the MWR is equally used in the following). No attempt, whatsoever, is made to discuss/evaluate/assess sensitivities [of] any details of the observational procedures (settings, post-processing, etc.). So, I think this paper has certainly not been submitted to the right journal. However, due to its other weaknesses, I cannot even propose to transfer it to another (Copernicus) journal.
• 2) The problem of i) the definition of a boundary layer height in the type of terrain the authors have chosen (some people call it Mountain Boundary Layer, MoBL, see major comment 3), ii) it’s measurement and iii) it’s modeling is indeed challenging. One of the generally accepted characteristics of the MoBL is its spatial variability. In this sense, 1 day (two radio soundings (one in the morning, one in the evening,  e., not even at least two ‘cases’ to repeat the experience), 13 hourly averaged outputs of microwave radiometer and the same number of data from a DWL) at one location cannot produce any robust results. Certainly not if we don’t even learn what weather conditions were prevailing on September 29 (the year is unfortunately not reported) in the region. But even if we knew this, the 13 data points cannot yield any statistical evidence. If more data were available (several months at least, depending on the season) the results could be made more statistically robust. And even the different measurement principles could be compared: why is the MWR temperature profile in Fig. 5a,d almost 5-10 K too cold in the first 1500 m agl, exhibits a much too strong gradient aloft, and why does it show a much higher ‘layering’ in the BL (when many other studies regret the MWR’s missing vertical resolution)? Could this have anything to do with the settings (for the MWR) the authors have used in the first place? What would different settings yield?, etc. etc. The RS, on the other hand, does usually not go ‘straight up’ – so, what does this make in a spatially inhomogeneous environment (see Fig. 11) with the measurement (and why is it better reproduced by a model that has some horizontal averaging)? An alternative measurement strategy could be to ‘move the instrument around’ (of course, having many instruments would be even better – but also expensive), deploy it in different valleys/basins, etc. and work out the instrument’s ability to measure a useful height, which corresponds to either the local CBL height or the MoBL height. Again, this would require a much longer data set, in order to obtain any robust statistics.
• 3) Definition of the topic. In the title/abstract it is always the ‘boundary layer’ (BL) that is being referred to (with the boundary layer height as the topic of interest) – but the BL has two dominant states, convective and stable – and the present analysis only concentrates on the unstable situations.Furthermore, the title suggests that in this paper the diagnostics of the Mountain Boundary Layer height (MoBL, Serafin et al., 2018) is of interest (which also has two different states, of course). In the Serafin et al paper, a reference is made to a companion paper, doi: 3390/atmos9070276), in which a definition of the MoBL is proposed. In the introduction (l.74) it is stated that ‘Mountainous terrain modifies the structure of the CBL ….’ (what again also would apply to the SBL, i.e., stable BL), btw. So, overall the introduction (and title/abstract) should make it very clear whether the topic of the paper is the MoBL height or the BL height in general and whether the focus is on unstable conditions or general BL states. The problem with the present study is, that it wants to investigate the degree to which model parameterizations (which are not expected to work well over mountainous terrain – they have all been developed for flat terrain) can reproduce atmospheric profiles (temperature, humidity, wind) which were measured with instruments that were also developed for flat terrain (the MWR, for example: has it been calibrated using local data as in doi: 10.5194/amt-8-3355-2015?) and cannot be expected to be spatially representative. And then, their ability to detect a characteristic location (BLH), which is only tentatively defined is assessed. This is simply too much of uncertainty for only one day of data. If longer data were available, one could systematically assess the accuracy of the measurements (possibly even improve/optimize the retrieval), then use very high resolution simulation (LES) to assess ‘the truth’, compare it to other sources of information, etc.
• 4) Section 4.3Here, the authors compare each BL scheme against two different data sets. So, if a scheme is ‘good’ as compared to one and ‘bad’ against the other: does this say anything about the quality of the scheme? (and what does it say about the quality of the observations?). Also, this comparison is made only for daytime conditions (what I ‘detect’ in the caption of Fig. 8) – so, it only applies (if at all) to unstable BLs. The ‘conclusion’ of this section then reads: ‘Overall, the fitting accuracy between MWR observational data and model predictions was generally higher than that of WPR, which may be attributed to differences in the measurement principles and accuracy of the two instruments’. What differences in the measurement principles do the authors refer to? Which aspect of accuracy? Do the authors want to imply that a measurement which produces better correspondence to a parameterization is a better measurement? Couldn’t it be so that the measurement principle is based on ‘flat terrain’ boundary layers (as the ABL schemes are as well) – but these do not hold in complex terrain?
• 5) Statistical analysis (Fig. 8) and Taylor diagram (Fig. 9) are not conclusive at all with so little data. The same is true for the box plots (Fig. 10). One day can be used as a case study – but then we would want to have different options analyzed, for example in the parameter settings of the MWR (e.g., layer depth, output frequency to mention the simple ones; updated/local/improved retrieval), or different variants of BLH retrieval (e.g., for the DWL), etc. etc. Then, a longer period (and/or other locations) are required to generalize the results.
• 6) Attribution of times/dates: it is stated that Sept 28/29 (no year given!) are modelled, with 12 hrs spin-up. So, is Sept 28, 0000 to 1200 (UTC? LT?) spin-up? If RSs are launched at 7 / 19 (LT), this would then mean that 2 19.15 soundings had been modelled and one 07.15 sounding. Still, in most of the figures, it is not indicated which date is referred to.
• 7) Attribution of heights: The RS is taken as a reference, but the various layer heights (and their interpretation) is given without reasoning. While the BLH is stated to be diagnosed from a bulk Ri criterion (the threshold for which is not referenced, discussed or investigated), what the authors call the ‘residual layer’ is simply assumed to be a RL (wouldn’t we have to look at the previous day’s BL for this?) and what the authors call the aerosol layer is i) not defined what it is, and ii) not mentioned based on what this attribution is made. For the former (i.e., the RL) we note here that (which corresponds to the order of magnitude of a gradient we often assume as the background stability) – and not the near-neutral stratification as implied by the textbook characteristics of an RL.

Minor comments

1. 18 ‘…during complex mountainous conditions’: in my understanding, mountains are usually rather persistent. So, it is probably rather ‘at locations with dominant complex mountainous influence’ or ‘during flow conditions dominated by upwind complex mountainous influence’.

l.79        please complete the Kamara (2020) reference.

l. 158     this sentence is repeated.

l.164 Tab.1 does not seem to be referenced in the text. So, either delete it or state why it is necessary.

l.166      ‘BLH from observed methods’: I don’t think the BLH can be determined from ‘observed methods’ (it is determined from profiles obtained with different observational methods)

l.187      ‘At 1600 m ….’ I think these heights should be labelled as ‘agl’ (above ground level) throughout (i.e., also in the axis labelling of, e.g. Fig. 2). If the height of the surrounding terrain plays such an important role, this is relevant.

l.189      ‘…and is indicated….’. Moreover, based on what (methodology, criterion) is the attribution (inversion at 1600 m agl → residual layer, 2600 m → aerosol layer) being made? Finally, the aerosol layer  has not been introduced (nor has the RL – but maybe this can be assumed to be known).

l.214      black triangles (that’s how they look like in the figure).

l.217      ‘overestimates the result’: this implies that the RS is correct….

l.219      …connecting red triangles…’: the triangles are black.

l.220      also the date (Sept 29) must be indicated.

l.244      ‘….is as follows’: nothing follows ….

l.245      ‘the study’ has developed a new algorithm: which study? The one cited? Or the present study? If the former this must become clear, if the latter, the ‘new algorithm’ must be detailed – not only showing the final results (Fig. 4), but also discussing assumptions (choice of thresholds, etc), sensitivities, etc.

l.249      the dashed black lines appear to be white in the figure…..

l.253      ‘RL fragmented from the previous day….’:  which area is identified as the RL? And based on what?

l.270      why using the one profile which is different as a ‘reference’? can the authors explain?

l.287      what is hourly instantaneous data? Either it is instantaneous or it is hourly (averaged). Do the authors mean ‘instantaneous at every hour? If so, why then do they think that an average over the hour is good for comparison? Can the authors explain?

l.288      I am not sure whether Fig. 6 shows a correlation (certainly not a value of 0.94). Also, the correlation is denoted ‘R’ here, while ‘R’ was used to denote mixing ratio so far (e.g., l. 265 – and many more. In the conclusion (1) even in the same sentence).

Fig. 6      what is labelled WMR (red squares) should probably mean MWR….

l.313      ‘…as illustrated in Fig. 7….. closely mirrors…’: does this come as a surprise? Basically, the figure shows that the BLH diagnostics are correctly implemented. (I think, this figure can easily be deleted).

Fig. 8, caption   Needless to say ‘shows’ – figures are usually used to show some data or results.

l.390      ‘…in Fig. 1a’: the authors probably want to refer to Fig, 2a. Moreover, based on what is the temperature gradient at 2600 m agl identified as a ‘clear aerosol layer structure’ – and for example that at 1600 m agl not?

Fig. 11    caption: using ACM2 schemes: how many are there? Figure: why are the panels 1 degree (E) / 2 degrees (N) smaller than that in Fig 1b? With this we have no chance to relate the presented results to the orography.

Review of "Comparative Evaluation of Boundary Layer Height Estimation Using Multi-Source Observations and WRF Simulations under Complex Topography” by Jinhua Zhong, Debin Su, Zijun Zheng, Yunong Xu, Wenyu Kong, Peng Fang, and Fang Mo.

The study uses boundary layer height observations collected by radiosonde, wind profile radar, and microwave radiometer in a complex (mountainous) terrain at a single site in China to evaluate the performance of different boundary layer parameterization schemes available in the WRF model. 

Overall, the manuscript is written in much detail which is appreciated but lacks significant scientific rigor, especially in terms of testing the methods followed to define the boundary layer height from different instrumentation. The topic of the manuscript, however, is of extreme importance as numerical models now are capable of running at high horizontal grid resolutions (~1-3km) for real-time forecasts. Any improvement in the model parameterization or identifying the need for it would benefit the modeling community. I see two major shortcomings in the study; 1) the way the manuscript is presented lacks novelty, and 2) using single-day observations does not account for any variability or seasonality and so is statistically insignificant to generalize the WRF model performance. The manuscript barely fits the scope of AMT as the primary objective of the work is to test the model parameterizations only and not present new or improved techniques for capturing the proper PBLH. The manuscript needs multiple major revisions before being considered for publication in AMT. 

A recent study (Wang et al. 2025) tests the WRF PBL parameterizations over Sichuan Basin, whose terrain complexity and features are very similar to the location presented in this study. Another study (Singh et al. 2024) presented the WRF PBL schemes’ performance over complex mountainous terrain, in the Himalayan region. Other such studies evaluated WRF over complex terrain using observations collected over a wide range of background conditions. Wang et al. (2025) used observations from 28 days and Singh et al. (2024) used observations over 5 day period to evaluate the PBL depths simulated by the WRF model.

Other comments:

1. The methods followed for evaluating the PBLH were not tested for their sensitivity to the chosen thresholds. For example, the radiosonde profiles were subjected to a 1.25 bulk Richardson number (Rib) threshold which doesn’t match with the threshold value in any of the PBL schemes considered that use Rib for PBLH determination. How would the statistics change if the respective Rib thresholds were used for profiles in Figure 2 based on the YSU and ACM2 schemes?
2. Line 245: “...new algorithm…” This is part of the manuscript that fits the scope of AMT. However, not many details were given about the robustness of this new algorithm. Further, it is not validated against the ground truth. It is mentioned that the WPR method used constrains the change in PBLH so that unrealistic PBL growth/decay rates are not captured. What is this rate and how did the authors choose this value?
3. MWR method uses a gradient threshold value of 2.75 K/km. What is the rationale for choosing this value? As referenced in the manuscript, Dai et al. (2014) concluded that different gradient values exist based on the type of the boundary layer and conditions at the top of the boundary layer.
4. Estimate observation-method-based PBLH from the WRF output and compare it against the respective observations. This way the model uncertainty in simulating the meteorological fields could be addressed. As it is presented, there is no single ground truth against which the methods can be evaluated. 
5. The emphasis is on complex terrain meteorology but the authors did not present or evaluate the model performance in capturing the topographical forcing on the atmospheric state, which often modulates the PBLH in the affected region. Cross-section plots of thermodynamic and wind variables would provide information on the presence of any slope/valley winds etc.

References:

Wang, Q., Zeng, B., Chen, G. and Li, Y., 2025. Simulation performance of planetary boundary layer schemes in WRF v4. 3.1 for near-surface wind over the western Sichuan Basin: a single-site assessment. Geoscientific Model Development, 18(5), pp.1769-1784.S

Singh, J., Singh, N., Ojha, N., Dimri, A.P. and Singh, R.S., 2024. Impacts of different boundary layer parameterization schemes on simulation of meteorology over Himalaya. Atmospheric Research, 298, p.107154.