the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
Impact of the Atmospheric Boundary Layer Height on the Concentration of Chemical Species in Numerical Model Simulations
Shuzhan Ren
Craig A. Stroud
Abstract. The top of the atmospheric boundary layer (ABL) serves as a boundary separating turbulent air in the ABL and free atmosphere in the troposphere. The increase/decrease of the ABL height (ABL-H) can dilute or concentrate chemical species in the ABL. In numerical simulations the ABL-H is involved in computing the vertical diffusivity and the counter-gradient term under the unstable condition in ABL parameterization schemes. Therefore, uncertainties in the ABL-H due to the uncertainties in meteorological fields and different definitions can affect the numerical predictions of the concentration of chemical species. To understand the impacts, a 1-D diffusion model with the K-profile scheme and an 3-D air quality forecast model with the turbulent kinetic energy (TKE)-based scheme are employed to examine the sensitivities of diffusion coefficient,counter-gradient term and tracer's concentration to the ABL-H analytically and numerically. Sensitivity tests with the 1-D model show that the increase/decrease ofthe ABL-H leads to the decrease/increase of concentration of tracers under both stable and unstable conditions due to the increase/decrease of the volume of air within the ABL. Under the unstable condition, the increase/decrease of the ABL-H also enhances/weakens the vertical diffusivity, and leads to the decrease/increase of the concentration of tracers for negative/positive vertical gradient of tracer. The impact of the ABL-H through the counter-gradient term is much smaller than the impact through changing the volume of trace and vertical diffusivity in the ABL. Sensitivity tests with the 3-D numerical model with the TKE scheme show increase/decrease of the ABL-H leads to strong/weak vertical diffusivity, but hasvery small impact of the ABL-H on the concentrations of pollutants over urban centers for the ABL-Hs which is defined based on the Richardson number and temperature.
Shuzhan Ren and Craig A. Stroud
Status: final response (author comments only)
-
RC1: 'Comment on acp-2023-37', Anonymous Referee #1, 06 Mar 2023
The manuscript describes some aspects of the sensitivity of simulated concentrations to the estimate of ABL height in certain boundary layer schemes. The title is misleading. The presentation is unclear and confusing. There may be some useful material here for certain specific users, but I do not see a path to acceptance for anything like the current form of this material.
General comments:
1. The title is misleading. The material is really about the errors incurred when the BL height is estimated incorrectly in certain kinds of schemes. Those errors are more or less serious depending on the scheme.
2. The authors do not seem to have a broad perspective on what is actually in use in models other than those of their own agency. Two types of mixing schemes are examined. Many of the errors noted are not significant problems in most state-of-the-art schemes. Even within this preprint, the errors in the TKE scheme are much less significant than in the K-profile scheme. This is an argument for not using the latter type of scheme, but that is never stated clearly.
3. The conceptual picture of the boundary layer presented here is oversimplified. The top of the ABL is not a material surface. It does not generally "serve as a boundary" (abstract). It is somewhat more acceptable to say that it is "a parameter describing the vertical extent of turbulent mixing" (Introduction), but then in the very next sentence the term "capping lid" is used. There are special times and places when the ABL top is well-defined and significantly impedes vertical mixing, and it happens that those are the conditions of most interest to the understanding of photochemical ozone pollution. A simple example of the more general situation: The "top" of a stable boundary layer is the point at which a more or less linear decrease of turbulence intensity reaches some selected threshold (becomes small enough). There is extensive recent literature, including review articles, describing the real boundary layer.
4. Presentation: Many aspects of the presentation are unclear. There are many equations, derived under different sets of assumptions. There is little overall concept or structure to guide the reader.
5. The key claim of the paper is buried at the end of section 2: "Under the unstable condition, the ABL-H affects tracer's concentration by changing the vertical diffusivity. This impact depends on both surface flux and the vertical gradient of tracers." This is generally true, but needs some qualification. Within a broad range, the exact value of K does not change tracer profiles significantly. Enough mixing is enough, unless there is some relatively strong competing process, for example large surface flux or large entrainment flux. Similarly, the value of K does not necessarily change the BL height if the stability gradient at the top is strong enough. In other words, the impact of a change in K is non-linear and depends on the stability profile.
Specific comments:
1. line 203: This is an instance of the conceptual problem noted in General item 3 above. The diffusivity need not be zero at the BL top; that is not a generally useful definition. It may be relatively small depending on the situation.
2. line 250: The heat flux does not jump suddenly at sunrise in reality. It is a smooth function of time. The emissions from traffic, however, are not very smooth. What is happening here is that the morning rush hour happens about the same time as the morning transition of the BL. Their relative timing depends on the season, among other things.
3. line 299: This is an example of General item 5 above. Many other factors contribute to the relationship between diffusivity and concentration. That is, after all, why we have models.
Citation: https://doi.org/10.5194/acp-2023-37-RC1 -
RC2: 'RC2', Anonymous Referee #2, 22 Mar 2023
This work presents the results of numerical simulations, which are parameterizations of more complex mechanisms at play in the atmosphere, and tries to give a general sense of how turbulent diffusivities and scalar concentrations depend on the height of the atmospheric boundary layer height (ABL-H). This is an important topic, but the results presented are merely those from a model, employed with several severe simplifications, entirely untethered from observed reality, and as such I recommend that it be rejected. Perhaps there is another journal that focuses solely on numerical modeling that might find it appropriate for their readership, but because this work makes no assessment of how it pertains to observations, I cannot see its utility to the ACP readership.
Major Concerns:
There are many other major concerns I have with this work that also indicate it is not ready for publication. First, there is an incomplete mention of the literature of scientists who have presented these kinds of relationships between ABL-H and scalar concentrations (most notably Schäfer et al., Meteorologische Zeitschrift, Vol. 15, No. 6, 647-658, December 2006; but also including, Yuval et al., Atmospheric Research 231 (2020); Wagner & Schäfer, Urban Climate 22 (2017) 64–79; Rigby & Toumi, Atmospheric Environment 42 (2008) 4932–4947.)
In my opinion there are too many figures (20 in total) and too little mechanistic understanding of the results presented. Gradient initial conditions (alpha) are compared, as are boundary layer maximum heights, as are diurnal flux patterns, as are different cities, as are ABL-H detection algorithms. The presentation seems unfiltered in terms of which variables are being altered over which range and for what reason and to what conclusion? Originally there are two flux patterns presented, one CO2-like and one H2O-like. But then later results are presented for CO and NOx (not shown) which have very different surface flux diurnal behaviors, making it very difficult to consider the model results in the second part of the paper in light of the first half.
The study is extremely specialized and specific so it is very hard to come away from it with any sense of how general it might be, or how its results might apply to any other situation. For instance, the work explicitly ignores the entrainment fluxes of all of these scalars. That omission, in and of itself, makes me weary of applying any of its conclusions to any particular circumstance in the real atmosphere.
I am unable to grasp why it is important to discern which parts of a parameterization (non-local/counter-gradient, diffusivity, dilution) are changing concentrations in a dynamic boundary layer (dzi/dt > 0). Why does that matter? Moreover, a changing boundary layer height is nearly synonymous with an entrainment flux (except in the case of purely divergent or convergent ABL flow with no turbulence at the ABL top.) That is, changes in ABL-H are mechanistically linked to entrainment fluxes (not always a diluting effect, by the way, consider CO2 over remote continental regions for example), so how can it be justified to ignore entrainment fluxes in all of this analysis? (See major concern above). In other words, the artificial isolation of using only variations in h and its impact on the counter-gradient term and diffusivity seems like it is not all that informative if changes in h are always coupled with concomitant changes induced by entrainment.
Because you are using the archetypes of CO2 (scheme 1) and H2O (scheme 2), the former being a top-down diffusion process in remote continental growing seasons, and the latter being typically bottom-up diffusion, then why not use the top-down and bottom-up diffusion schemes in this analysis? I realize that Holtslag & Moeng (1991) discuss eliminating this in some generalized cases, but they do admit, “Overall it is seen that the impact of entrainment flux cannot be neglected.” (See their Equations 25a,b).
Specific Concerns:
p.4, line 87: 500 Wm-2 is an incredibly large surface sensible heat flux. For example, summertime peak H0 in Yuma, AZ is about 250 W/m2.
p.5, line 110: Phi_M is typically reserved for the surface layer similarity dimensionless shear function, and Phi_H is the dimensionless temperature gradient function.
p.6, eq. 2-9: This vertical gradient term (alpha) is not a free variable. It is determined by the bottom-up and/or top-down gradient functions. I realize that in this work alpha represents this initial condition, but why would it matter where the model starts the value if it is different from that throughout most of the day? Moreover, Fig. 1 from Moeng & Wyngaard (1984) shows that alpha is a strong function of elevation (z) in the surface layer.
p.6, line 142: Traditional K-theory in the neutral surface layer yields K(z) is an approximately linear function of z. Even Holtslag & Moeng (1991) show this to be the case. How is a constant K with height relevant?
p.9, line 159: Fig. 3a indicates that K increases quite rapidly in early morning and evening. Maybe it is not clear exactly what times of day are being considered in this discussion.
9, line 164: How can you justify that alpha should be correctly reproduced in time in your model? Surely the gradients are established by the surface and entrainment fluxes (cf. Wyngaard & Brost, 1984), which your model has as a function of time of day. But for simplicity you say that you have neglected entrainment fluxes. The exact timing of these changes then seems somewhat arbitrary as alpha is really only relevant at t=0.
p.9, line 176: The comparison of percentage increase/decrease of mixing ratios is not very generalizable because an arbitrary constant (420 ppm) is being subtracted. If 400 ppm had been used as the offset these percentages would all change, so it is not a very meaningful result that can be generalized by a reader.
p.9, line 178: It would be much more descriptive and easier for a reader to follow if a term like CO2-like surface flux scalar, or H2O-like surface flux scalar, were used instead of the arbitrary terms ‘first’ and ‘second’.
p.9, line 179: I do not see Figure 8 resembling Fig. 2d much at all.
Figure 8: There is very little information in this figure. All four panels look indistinguishable, so I am not sure it is telling the reader anything outside of the fact that the results are insensitive to the arbitrary initial condition of scalar gradient. In any event, some discussion of this feature of the figure warrants mentioning.
p.10, Eq. 3-1: Where is the shear production (~ u*3/z) in this TKE budget equation? Under neutral to stable conditions this equation cannot sustain any turbulence whatsoever. Yet you have u* in your boundary condition for E.
p.10, line 199: Yes, but surely just above these heights the TKE, and therefore K, goes to zero. I see these values as just representing a slight uncertainty in the ABL-H.
Fig. 10: There is no mention of what the origin of the information in this graph is, nor what the units are. I am assuming this is from a model run, but under what meteorological conditions is never mentioned or referred to. In these urban areas, I would suspect that the shear production is, all else being equal, even more important to the sustenance and character of the turbulence due to the “rough” character of urban landscapes.
p.21, line 235: It would be helpful to know what the surface flux diurnal profile looked like for these simulations (“first” or “second” type, or presumably if it is CO and NOx, it is different from either of those), and what are the different amounts for each domain? There is no mention of anything about these model runs so they are very difficult to contextualize.
p.21, line 242: Is there any information to be gleaned from the four different cities? Why does one have smaller or larger r-values? Why show the different cities if there is nothing to observe from it, especially since they are just simulated cities anyway without any knowledge of their relative emissions or geography or meteorology.
p.21, lines 249-251: Why is the mentioned positive correlation not apparent in Fig.11?
Figure 13: These CO diurnal profiles do not look like any that I have seen before. There must be a diurnal pattern to your emissions (rush hours) which normally imprints a bimodal shape on the CO diurnal pattern because the edges of rush hour tend to occur when mixing is weak (early a.m. & early evening.) See for example, Yassin et al., Environ Monit Assess (2018) 190: 372, https://doi.org/10.1007/s10661-018-6737-9.
p.21, line 257: What does this intercity variability tell us? It is one thing to report this in a set of observations, but to present it with model results without having any conjecture as to why does not seem very informative to a general readership.
p.23, line 263: Concentrations depend on ABLH and emission fluxes (assuming the chemistry is slow with respect to this small-scale mixing.) It is therefore imperative that you describe the surface flux pattern for these sensitivity studies.
p.24, line 288: I am not sure what the merit is in discussing NO2 when you do not present any of the data. It is similar to CO in some cases because its dominant source is probably the same: internal combustion. But NO2 exchanges with O3 + NO on a timescale of minutes (faster than a lot of the dynamics under consideration here), so it is not going to be conserved upon mixing, it is going to react to changes in O3 and sunlight in a way that CO will not.
Citation: https://doi.org/10.5194/acp-2023-37-RC2
-
RC2: 'RC2', Anonymous Referee #2, 22 Mar 2023
Shuzhan Ren and Craig A. Stroud
Shuzhan Ren and Craig A. Stroud
Viewed
| HTML | XML | Total | BibTeX | EndNote | |
|---|---|---|---|---|---|
| 219 | 64 | 8 | 291 | 3 | 2 |
- HTML: 219
- PDF: 64
- XML: 8
- Total: 291
- BibTeX: 3
- EndNote: 2
Viewed (geographical distribution)
| Country | # | Views | % |
|---|
| Total: | 0 |
| HTML: | 0 |
| PDF: | 0 |
| XML: | 0 |
- 1