Revised Comments on:


Extraction of geopotential height and temperature structure from profiler and rawinsonde winds


S. Businger, M.E. Adams, S.E. Koch, and M.L. Kaplan

Submitted as Correspondence


Charles A. Doswell III

Cooperative Institute for Mesoscale Meteorological Studies, Norman, OK


Monthly Weather Review

August 2001

Revised: November 2001


Corresponding author address: Dr. Charles A. Doswell III, CIMMS, University of Oklahoma, 100 E. Boyd St., Room 1110, Norman, OK 73019. E-mail:

NOTICE: This manuscript has been submitted to Monthly Weather Review, and copyright is to be transferred to the AMS; see their policy statement. There may be differences between the paper as it appears here and the final version, owing to revisions suggested by the reviewers.

In a recent paper, Businger et al. (2001; hereafter B01) demonstrate the application of a technique employing the full divergence equation to derive heights and temperatures from wind information. Their stated main goals include the wish to demonstrate the feasibility and validity of using the full divergence equation, as opposed to other similar schemes using truncated forms of the divergence equation.

Development of methods to use wind fields alone to derive estimated thermodynamic information is of considerable importance at a time when the value of rawinsonde observations has been a matter of some debate and concern (e.g., Bosart 1990). In fact, it is suggested in B01 that the cost of asynoptic rawinsonde ascents is "prohibitive" and this argument implies that the development of thermodynamic "retrievals" is a critical need. I am not questioning the need for retrieval techniques, but I certainly think that the use of the term "prohibitive" to describe the costs of asynoptic rawinsonde data is arguable. The existing regional network of operational wind profilers has never been implemented nationally, perhaps in no small part because wind profilers have not proven to be the low-cost option to in situ measurement systems that their early advocates proposed them to be (e.g,, Hogg et al. 1983). The incremental cost of asynoptic observations in addition to the routine times at 00 and 12 UTC at the regular rawinsonde sites is the most relevant cost, not the total cost associated with the routine operation of the site. Of course, the costs of adding new rawinsonde sites would clearly be substantial and certainly are considered "prohibitive" by some, especially in view of the costs incurred by numerous recent site moves. It is noteworthy that during possible severe weather outbreaks, it is common for forecasters to request 18 UTC special soundings at selected sites, primarily to obtain thermodynamic variables not directly observed by the profilers.

In no way do my comments on this minor wording issue detract from the value of wind profilers, which clearly is substantial. Nevertheless, the current failure to expand the profiler network is almost certainly explained at least in large part by the de facto "prohibitive" cost of installation and operation of new profiler sites, in spite of their demonstrated utility. This issue aside, however, I certainly agree there is a need for thermodynamic retrievals from wind observations.

B01 considers only a single case study, so this work alone cannot be considered a conclusive test of their proposed technique. Rather, their generally positive results are but a first step in what should be a more substantial test than can be offered from any one case study. The authors state that they chose this case (at least in part) because of the asynoptic rawinsonde data available. Although I see some procedural flaws in this work, to be developed in what follows, I don't view those flaws as being sufficient by themselves to obviate the major conclusions drawn in B01. Rather, it seems to me that the authors have ignored several options by which their study could have been made more convincing, assuming that my suggested changes in the methodology would have the effect of further supporting B01's case study results. I have three primary concerns with the execution of this study.

The first problem I see is that the authors have chosen not to make any use of the direct vertical velocity measurements made by the profilers' vertically-pointing beam. They acknowledge the well-known fact that those measured vertical winds are used in the algorithms by which the horizontal winds are derived from the profiler observations. However, they argue that they did not use those measured vertical motions because (a) ignoring them is consistent with scale of the analysis, (b) the vertical motions are noisy, owing in part to subgrid-scale vertical drafts and to rainfall contamination, and (c) the fact that rawinsondes do not provide vertical motion, either. I find all of these arguments unconvincing regarding the omission of these data from the analysis.

If the vertical motions are too noisy to include in the analysis, why are they nevertheless acceptable for the derivation of the horizontal winds? The fact is that any "noise" in the vertical motions, whatever its origins, must have affected the horizontal motion calculations, as well. There are straightforward ways to eliminate the effects of rainfall contamination from the data, as well as techniques in objective analysis to account for the noise inherent in any set of measurements. Since objective analysis schemes generally have low-pass filter characteristics (see Stephens 1971), the scale of the analysis can be chosen by an analyst who is familiar with using the methods of objective analysis, irrespective of the presence of "subgrid" scale input in the data. There is subgrid-scale noise present in virtually all observations, but this is not typically used as a reason to ignore the data!

The fact that rawinsondes do not include vertical motion measurements is no justification for ignoring vertical motion observations if they are available. This is comparable to arguing that we should ignore the rawinsonde's thermodynamic observations because the profilers don't have them!

Thus, I see no good reason to have excluded the observed vertical motions from the analysis. Of course, including them substantially complicates the analysis and the vertical motions must be made consistent with the horizontal divergence via the mass continuity equation. Some considerable additional effort would be required. However, I think it is quite possible that the inclusion of those observed vertical motions might have improved the overall analysis. At the very least, the authors could have tried using the vertical motion observations and convinced themselves (and shown their readers) whether or not the observed vertical motions would have improved the resulting analysis. The quality of the input analysis to the retrieval scheme surely is an important component in the effort to make a case on behalf of the scheme. I'll return to this theme when I make my third point.

Second, the rationale for choosing this particular case apparently is that STORM-FEST has provided something special by having 3-hourly soundings. These asynoptic soundings provide the opportunity for an interesting validation test, by comparing the results from (a) using all the data, which is what the authors did, and (b) using all the data except for the 3-hourly soundings . The authors have available what amounts to an independent measurement of the height and temperature structure at the times and locations of the 3-hourly soundings. Since the sounding thermodynamic data are not included in the input to the scheme, omitting these special soundings only removes their wind observations when the technique being proposed in B01 is applied. Not using the wind data as input from the few special soundings would almost certainly represent only a slight degradation of the final wind field analysis. This probably would produce an associated small degradation of the retrieved height and temperature fields. However, I believe it to be of considerable interest to compare the retrieved soundings at the sites and times of the special soundings with the actual observed soundings in case (a) and especially in case (b)..

I want to emphasize that the magnitude of the analysis degradation is not the main point of my concern. Rather, the undone comparison I've proposed in case (b) represents a potentially revealing test of how well the standard data, including the standard rawinsondes and the profilers (but not the special soundings), would be able to reproduce the observed thermodynamic profiles at those special sounding sites, in the absence of those soundings. The value of this seems so obvious to me, I believe it represents an important missed opportunity to enhance the credibility of their technique.

Finally, I'm concerned that the authors have chosen not to use a proven method to improve the quality of their divergence estimates based on the wind field. Beginning with Bellamy (1949), through Ceselski and Sapp (1975), Schaefer and Doswell (1979), Doswell and Caracena (1988), and most recently Spencer and Doswell (2001), it is becoming ever more obvious that the standard method of estimating derivatives, by first mapping the wind observations onto a regular grid and then using finite differences to estimate the derivative fields, is substantially inferior to line integral methods for estimating those derivatives. Recent results presented by Spencer and Doswell (2001) show that the inherent superiority of line integral methods for derivative estimation is substantial even at "well-sampled" wavelengths, thus correcting an assertion made in Doswell and Caracena (1988). These findings demonstrate that the advantages of line integral divergence estimation in cases where the spatial sampling is not uniform are not limited to short wavelengths.

One simple form of the line integral technique is described as the "linear vector point function" method in Zamora et al. (1987), a paper referenced in B01. In their section 3, in fact, the authors of B01 argue that this improvement of the divergence estimates associated with using line integral techniques is actually of little significance, citing results shown in Karyampudi et al. (1995; hereafter K95). K95 is not devoted to issue of objective analysis, but rather is concerned with other issues. The comparison of the two methods within K95 is quite brief and their interpretation of the results to the effect that the methods are comparable is most definitely arguable. My interpretation of the presentation in K95 regarding this comparison of analysis methods is that K95's results are quite consistent with other studies (e.g., the aforementioned references) comparing the two techniques. That is, I see their results as validating the notion that the standard method's ability to estimate divergence is markedly inferior to line integral methods. Since the divergence estimates are the input for this proposed technique, anything that improves the quality of the estimated divergence should strengthen the case being made in favor of the technique. I am disappointed that the authors have not chosen to use the best available divergence estimates possible when evaluating their proposed retrieval scheme.

I conclude that the authors have not made the most convincing arguments in favor of their proposed method for retrieving thermodynamic information from wind fields that are possible, using the data they had available. My hope is that in future validation studies of their technique, the issues I've raised will be given due consideration.



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