the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 03 Jan 2024
Shallow boundary layer heights controlled by the surface-based temperature inversion strength are responsible for trapping home heating emissions near the ground level in Fairbanks, Alaska
Abstract. In cold climate cities, like Fairbanks, Alaska, during winter, reduced vertical mixing in the atmosphere leads to pollution trapping and concerningly high PM2.5 concentrations at ground level. To study pollution trapping, we simulated dispersion of SO2 from home heating emissions during the ALPACA-2022 field study in Fairbanks, Alaska using the Platform for Atmospheric Chemistry and Transport one-dimensional model (PACT-1D). Eddy diffusion coefficients that control vertical transport were parameterized by the near-surface temperature inversion strength according to stable boundary layer (SBL) theory and horizontal export was calculated from the wind speed. The model parameterized the SBL height as a function of the near-surface inversion strength, with the SBL height varying between 50 m for weak inversions down to 20 m for strong inversions. The model results were compared to long-path differential optical absorption spectroscopy (LP-DOAS) concentration profiles and in-situ observations of SO2 over the range of 3 m to 191 m above downtown Fairbanks over a 33-day period in winter and achieved excellent agreement (R = 0.88). Sensitivity studies showed that the model is most sensitive to the SBL height and the associated eddy diffusivity profile. Model-derived pollution residence times in Fairbanks are on the order of hours during winter, with a median steady state residence time of 2.1 hours under stable atmospheric conditions, indicating there is limited time for chemical processing.
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RC1: 'Comment on egusphere-2023-3082', Anonymous Referee #1, 31 Jan 2024
Review of the manuscript egusphere-2023-3082
Shallow boundary layer heights controlled by the surface-based temperature inversion strength are responsible for trapping home heating emissions near the ground level in Fairbanks, Alaska.
By Cesler-Maloney et al.
Summary:
This study uses observations from the ALPACA-2022 field campaign in Fairbanks (Alaska) to understand the evolution of the SO2 concentrations in stable boundary layers over the city. The dynamics of the atmosphere and the vertical dispersion of the SO2 is modelled in the PACT-1D single-column model to learn about what are the controlling factors of the SO2 profiles in time and height. Fairbanks is subject often to very stable boundary layers, which trigger high concentrations and health issues. I have several concerns with the study in terms of novelty, physical consistency, reproducibility, focus and organization.
Recommendation: reject
Major remarks:
- Research focus: my first concern is that the manuscript does not contain a well-defined research question. The introduction section is very long, while it does not include a proper review of SBL work done in the last 20 years (see later on about novelty), but it does not end up with a clear knowledge gap and a research question (or hypothesis) that will be answered (confirmed or refuted) in this study. The final stage of the Introduction announces what is going to be done as activities, but it lacks a constrained research question. Hence the focus needs to be sharpened. That is why the paper is also relatively long.
- Novelty: I find the study not novel. In my view the observations from the field campaign are new, and can offer insights. But the modelling work is building on studies done in the 1970s and 1980s, while much more insights have been developed later on. The K(z) parameterization that is being used has been developed for SBLs that are driven with relatively high wind speeds where the turbulence is well maintained, while in reality this is not the case, especially for shallow SBLs of ~50m or shallower that the authors study here. It is well know that the SBL has two regimes (e.g. Mahrt, 1998; Vogelezang and Holtslag, 1996), i.e. one (weakly stable boundary layer) where the turbulence is well-behaved and Monin-Obukhov scaling applies, and the very stable boundary layer where scaling does not work, and where other processes take over, like waves, longwave radiation divergence and so on. Alternatively a series of papers by Zilitinkevich categorized the SBLs in truly neutral SBLs, conventionally neutral SBLs, and long-lived SBLs. For each of them a diffusion transfer coefficient formulations have been built. The same holds for SBL height formulations. E.g. Steeneveld et al. (2007) developed an SBL height formulation that clearly distinguishes 2 regimes. None of this kind of archetyping is present in the submitted paper at hand.
- Physical consistency. I am concerned about the physical consistency of the meteorological forcings in the 1D model. If I understand it well the 1D model has a prescribed PBL depth (from the observed T profile in the mast) and friction velocity (0.4 m/s) and a non-evolving wind speed profile. The paper is quiet about whether potential temperature and humidity is prognostic or not, neither whether longwave radiation divergence is accounted for. Obviously the SBL depth a result of the evolving wind speed, surface friction velocity, temperature profile etc. Earlier studies showed the equilibrium SBL depth is roughly 700 times the friction velocity (see Vogelezang and Holtslag paper), or alternative expressions where h ~ u*. Here if h =700 * 0.4 means the eq PBL depth would be 280 m, which is much deeper than the shallow PBLs the paper discusses. So it appears that for many of the simulations one is in a unphysical range/domain for geowind, friction velocity and SBL height. If this is true the results are not meaningful.
- Reproducibility: I have difficulties following the single column model setup. As a single column model user, I need a roughness length (for momentum, heat and species), geostrophic wind (in height and time) speed, initial profiles, timestep, subsidence rate, advection of momentum, heat, and moisture. These are not reported. Perhaps it is good have a look at the GABLS3 model setup paper (Bosveld et al, 2014) that discusses all these forcing in detail. Moreover I miss a detailed model evaluation against the meteorological fields to show the model is trustworthy.
- Writing Style and organization. As said before the paper is too long, the Introduction is too long and not too the point. In the results section many paragraphs start with phrases like “Figure X shows a time series of….”. In terms if style it is not attractive. But also these sentences belong to the Figure caption, not the main text. In terms of organization, the paper first discusses some modelling (the academic cases), then it discusses in detail the observations and then it returns to the modelling. This is somewhat confusing. The conclusion section needs to be more concise and should focus on answering the well-defined research question in the Introduction Section.
Sorry I cannot be more positive.
Minor remarks
Ln 1: title is very long and not appealing
Ln 64: 40 nanomole/mole. Is that concentration a problem?
Ln 135: Obukhov length? Should it not be the local Obukhov length, as was learnt from Nieuwstadt 1984?
Ln 142: At this stage it is unclear how the SBL height is formally defined (based on TKE, inversion strength, LLJ height …)
Ln 177: co-added: vague. What did you precisely do?
Ln 225: The behaviour of 1D models depends on the first model height. Please report where it is?
Ln 242: Obukhov length. It is Monin-Obukhov theory, but the Obukhov length scale.
Ln 288: comparison with sonde data. Please quantify the scores. Models do have difficulties with forecasting SBLs, so “good agreement” is somewhat handwavy.
Ln 357: conceptual model should be part of the Introduction
Ln 373: Fig 4 is referred to before Figure 3.
Ln 453: 3-h averaging is very coarsening the data, and will help to raise the correlation. Is this fair?
Figure 1: I miss a scale bar and a north-arrow
References:
Bosveld, F.C., Baas, P., van Meijgaard, E. et al. The Third GABLS Intercomparison Case for Evaluation Studies of Boundary-Layer Models. Part A: Case Selection and Set-Up. Boundary-Layer Meteorol 152, 133–156 (2014). https://doi.org/10.1007/s10546-014-9917-3
Mahrt, L. Nocturnal Boundary-Layer Regimes. Boundary-Layer Meteorology 88, 255–278 (1998). https://doi.org/10.1023/A:1001171313493
Steeneveld, G. J., B. J. H. van de Wiel, and A. A. M. Holtslag, 2007: Diagnostic Equations for the Stable Boundary Layer Height: Evaluation and Dimensional Analysis. J. Appl. Meteor. Climatol., 46, 212–225
Vogelezang, D.H.P., Holtslag, A.A.M. Evaluation and model impacts of alternative boundary-layer height formulations. Boundary-Layer Meteorol 81, 245–269 (1996). https://doi.org/10.1007/BF02430331
Citation: https://doi.org/10.5194/egusphere-2023-3082-RC1 -
AC3: 'Reply on RC1 -- See unified reply', William R. Simpson, 22 Mar 2024
We have replied to both reviews in a single supplement that is attached to the editor's comment.
Citation: https://doi.org/10.5194/egusphere-2023-3082-AC3
-
RC2: 'Comment on egusphere-2023-3082', Anonymous Referee #2, 07 Feb 2024
The manuscript describes measurements and simple modeling of pollutant accumulation in Fairbanks. It has some strengths, and significant weaknesses. On balance I think it is not original or novel enough to be publishable in a first-rate scientific journal.
Strengths: An interesting and unusual dataset, with measurements well suited to the problem. For example, the finding that the concentrations measured by the tower were fairly representative of the long-path is a nice contribution. The measurements should be published, which does not seem to have happened yet.
Weaknesses: The main weakness is that the conclusions are already well known. Trapping of pollutants in a shallow boundary layer in a basin is obvious. The relationship between inversion strength and SBL depth is also not new. The 1D model is not particularly novel either. Such models have been used for decades, why develop another one? If the aim is to forecast polluted conditions, that can be done well enough for practical purposes using routine weather forecasts, informed by local knowledge.
Citation: https://doi.org/10.5194/egusphere-2023-3082-RC2 -
AC4: 'Reply on RC2 -- See unified reply', William R. Simpson, 22 Mar 2024
We have replied to both reviews in a single supplement that is attached to the editor's comment.
Citation: https://doi.org/10.5194/egusphere-2023-3082-AC4
-
AC4: 'Reply on RC2 -- See unified reply', William R. Simpson, 22 Mar 2024
-
EC1: 'Comment on egusphere-2023-3082', Michael Tjernström, 18 Mar 2024
This comment is intended to save time for everyone involved. Noting that no response has appeared since this discussion ended over a month ago, I have assessed the review comments from the two reviewers. One reviewer recommends rejection while the other, although not using this particular phrase, is also less than enthusiastic.
Given the nature of the two reviews, I would at this point lean towards recommend rejecting this manuscript. The comments are simply to many and grave that I feel it would be improduktive to try and remedy in revision. It would in my opinion be better if a completely new manuscript were to be submitted at a later date, making good use of these reviewers insight.
Michael Tjernström, Handling Editor
Citation: https://doi.org/10.5194/egusphere-2023-3082-EC1 -
AC1: 'Reply on EC1', William R. Simpson, 18 Mar 2024
We were previously given (via email) a deadline of 28 March 2024 to respond to reviews and will respond by that date. We are actively working on the responses and hope that the editorial decision will take into account our responses.
Citation: https://doi.org/10.5194/egusphere-2023-3082-AC1 - AC2: 'Reply to Editor and both reviews', William R. Simpson, 22 Mar 2024
-
AC1: 'Reply on EC1', William R. Simpson, 18 Mar 2024
Status: closed
-
RC1: 'Comment on egusphere-2023-3082', Anonymous Referee #1, 31 Jan 2024
Review of the manuscript egusphere-2023-3082
Shallow boundary layer heights controlled by the surface-based temperature inversion strength are responsible for trapping home heating emissions near the ground level in Fairbanks, Alaska.
By Cesler-Maloney et al.
Summary:
This study uses observations from the ALPACA-2022 field campaign in Fairbanks (Alaska) to understand the evolution of the SO2 concentrations in stable boundary layers over the city. The dynamics of the atmosphere and the vertical dispersion of the SO2 is modelled in the PACT-1D single-column model to learn about what are the controlling factors of the SO2 profiles in time and height. Fairbanks is subject often to very stable boundary layers, which trigger high concentrations and health issues. I have several concerns with the study in terms of novelty, physical consistency, reproducibility, focus and organization.
Recommendation: reject
Major remarks:
- Research focus: my first concern is that the manuscript does not contain a well-defined research question. The introduction section is very long, while it does not include a proper review of SBL work done in the last 20 years (see later on about novelty), but it does not end up with a clear knowledge gap and a research question (or hypothesis) that will be answered (confirmed or refuted) in this study. The final stage of the Introduction announces what is going to be done as activities, but it lacks a constrained research question. Hence the focus needs to be sharpened. That is why the paper is also relatively long.
- Novelty: I find the study not novel. In my view the observations from the field campaign are new, and can offer insights. But the modelling work is building on studies done in the 1970s and 1980s, while much more insights have been developed later on. The K(z) parameterization that is being used has been developed for SBLs that are driven with relatively high wind speeds where the turbulence is well maintained, while in reality this is not the case, especially for shallow SBLs of ~50m or shallower that the authors study here. It is well know that the SBL has two regimes (e.g. Mahrt, 1998; Vogelezang and Holtslag, 1996), i.e. one (weakly stable boundary layer) where the turbulence is well-behaved and Monin-Obukhov scaling applies, and the very stable boundary layer where scaling does not work, and where other processes take over, like waves, longwave radiation divergence and so on. Alternatively a series of papers by Zilitinkevich categorized the SBLs in truly neutral SBLs, conventionally neutral SBLs, and long-lived SBLs. For each of them a diffusion transfer coefficient formulations have been built. The same holds for SBL height formulations. E.g. Steeneveld et al. (2007) developed an SBL height formulation that clearly distinguishes 2 regimes. None of this kind of archetyping is present in the submitted paper at hand.
- Physical consistency. I am concerned about the physical consistency of the meteorological forcings in the 1D model. If I understand it well the 1D model has a prescribed PBL depth (from the observed T profile in the mast) and friction velocity (0.4 m/s) and a non-evolving wind speed profile. The paper is quiet about whether potential temperature and humidity is prognostic or not, neither whether longwave radiation divergence is accounted for. Obviously the SBL depth a result of the evolving wind speed, surface friction velocity, temperature profile etc. Earlier studies showed the equilibrium SBL depth is roughly 700 times the friction velocity (see Vogelezang and Holtslag paper), or alternative expressions where h ~ u*. Here if h =700 * 0.4 means the eq PBL depth would be 280 m, which is much deeper than the shallow PBLs the paper discusses. So it appears that for many of the simulations one is in a unphysical range/domain for geowind, friction velocity and SBL height. If this is true the results are not meaningful.
- Reproducibility: I have difficulties following the single column model setup. As a single column model user, I need a roughness length (for momentum, heat and species), geostrophic wind (in height and time) speed, initial profiles, timestep, subsidence rate, advection of momentum, heat, and moisture. These are not reported. Perhaps it is good have a look at the GABLS3 model setup paper (Bosveld et al, 2014) that discusses all these forcing in detail. Moreover I miss a detailed model evaluation against the meteorological fields to show the model is trustworthy.
- Writing Style and organization. As said before the paper is too long, the Introduction is too long and not too the point. In the results section many paragraphs start with phrases like “Figure X shows a time series of….”. In terms if style it is not attractive. But also these sentences belong to the Figure caption, not the main text. In terms of organization, the paper first discusses some modelling (the academic cases), then it discusses in detail the observations and then it returns to the modelling. This is somewhat confusing. The conclusion section needs to be more concise and should focus on answering the well-defined research question in the Introduction Section.
Sorry I cannot be more positive.
Minor remarks
Ln 1: title is very long and not appealing
Ln 64: 40 nanomole/mole. Is that concentration a problem?
Ln 135: Obukhov length? Should it not be the local Obukhov length, as was learnt from Nieuwstadt 1984?
Ln 142: At this stage it is unclear how the SBL height is formally defined (based on TKE, inversion strength, LLJ height …)
Ln 177: co-added: vague. What did you precisely do?
Ln 225: The behaviour of 1D models depends on the first model height. Please report where it is?
Ln 242: Obukhov length. It is Monin-Obukhov theory, but the Obukhov length scale.
Ln 288: comparison with sonde data. Please quantify the scores. Models do have difficulties with forecasting SBLs, so “good agreement” is somewhat handwavy.
Ln 357: conceptual model should be part of the Introduction
Ln 373: Fig 4 is referred to before Figure 3.
Ln 453: 3-h averaging is very coarsening the data, and will help to raise the correlation. Is this fair?
Figure 1: I miss a scale bar and a north-arrow
References:
Bosveld, F.C., Baas, P., van Meijgaard, E. et al. The Third GABLS Intercomparison Case for Evaluation Studies of Boundary-Layer Models. Part A: Case Selection and Set-Up. Boundary-Layer Meteorol 152, 133–156 (2014). https://doi.org/10.1007/s10546-014-9917-3
Mahrt, L. Nocturnal Boundary-Layer Regimes. Boundary-Layer Meteorology 88, 255–278 (1998). https://doi.org/10.1023/A:1001171313493
Steeneveld, G. J., B. J. H. van de Wiel, and A. A. M. Holtslag, 2007: Diagnostic Equations for the Stable Boundary Layer Height: Evaluation and Dimensional Analysis. J. Appl. Meteor. Climatol., 46, 212–225
Vogelezang, D.H.P., Holtslag, A.A.M. Evaluation and model impacts of alternative boundary-layer height formulations. Boundary-Layer Meteorol 81, 245–269 (1996). https://doi.org/10.1007/BF02430331
Citation: https://doi.org/10.5194/egusphere-2023-3082-RC1 -
AC3: 'Reply on RC1 -- See unified reply', William R. Simpson, 22 Mar 2024
We have replied to both reviews in a single supplement that is attached to the editor's comment.
Citation: https://doi.org/10.5194/egusphere-2023-3082-AC3
-
RC2: 'Comment on egusphere-2023-3082', Anonymous Referee #2, 07 Feb 2024
The manuscript describes measurements and simple modeling of pollutant accumulation in Fairbanks. It has some strengths, and significant weaknesses. On balance I think it is not original or novel enough to be publishable in a first-rate scientific journal.
Strengths: An interesting and unusual dataset, with measurements well suited to the problem. For example, the finding that the concentrations measured by the tower were fairly representative of the long-path is a nice contribution. The measurements should be published, which does not seem to have happened yet.
Weaknesses: The main weakness is that the conclusions are already well known. Trapping of pollutants in a shallow boundary layer in a basin is obvious. The relationship between inversion strength and SBL depth is also not new. The 1D model is not particularly novel either. Such models have been used for decades, why develop another one? If the aim is to forecast polluted conditions, that can be done well enough for practical purposes using routine weather forecasts, informed by local knowledge.
Citation: https://doi.org/10.5194/egusphere-2023-3082-RC2 -
AC4: 'Reply on RC2 -- See unified reply', William R. Simpson, 22 Mar 2024
We have replied to both reviews in a single supplement that is attached to the editor's comment.
Citation: https://doi.org/10.5194/egusphere-2023-3082-AC4
-
AC4: 'Reply on RC2 -- See unified reply', William R. Simpson, 22 Mar 2024
-
EC1: 'Comment on egusphere-2023-3082', Michael Tjernström, 18 Mar 2024
This comment is intended to save time for everyone involved. Noting that no response has appeared since this discussion ended over a month ago, I have assessed the review comments from the two reviewers. One reviewer recommends rejection while the other, although not using this particular phrase, is also less than enthusiastic.
Given the nature of the two reviews, I would at this point lean towards recommend rejecting this manuscript. The comments are simply to many and grave that I feel it would be improduktive to try and remedy in revision. It would in my opinion be better if a completely new manuscript were to be submitted at a later date, making good use of these reviewers insight.
Michael Tjernström, Handling Editor
Citation: https://doi.org/10.5194/egusphere-2023-3082-EC1 -
AC1: 'Reply on EC1', William R. Simpson, 18 Mar 2024
We were previously given (via email) a deadline of 28 March 2024 to respond to reviews and will respond by that date. We are actively working on the responses and hope that the editorial decision will take into account our responses.
Citation: https://doi.org/10.5194/egusphere-2023-3082-AC1 - AC2: 'Reply to Editor and both reviews', William R. Simpson, 22 Mar 2024
-
AC1: 'Reply on EC1', William R. Simpson, 18 Mar 2024
Data sets
Gas and meteorological measurements at the CTC site and Birch Hill in Fairbanks, Alaska, during the ALPACA-2022 field study William Simpson, Meeta Cesler-Maloney, and Ryan Hoskins-Chaddon https://doi.org/10.18739/A27D2Q87W
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