the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
The highfrequency response correction of eddy covariance fluxes – Part 1: An experimental approach and its interdependence with the timelag estimation
Toprak Aslan
Andreas Ibrom
Eiko Nemitz
Üllar Rannik
Ivan Mammarella
Download
 Final revised paper (published on 28 Jul 2021)
 Preprint (discussion started on 11 Jan 2021)
Interactive discussion
Status: closed

RC1: 'Comment on amt2020479', Marc Aubinet, 15 Jan 2021
General comments
This paper discusses different spectral corrections procedures for low pass filtering effects in eddy covariance systems. Despite eddy covariance has become the most common approach to determine, among others, CO2, water vapour or greenhouse gas budgets of ecosystems, the method still suffers from uncertainties due to random and, more worryingly to my opinion, to systematic errors. From this point of view each study providing a better understanding of measurements errors and improving correction procedure is welcome.
In that respect, the paper by Peltoli et al is important for at least two reasons: first it points a systematic error actually made by some eddy covariance data treatment softwares (including EddyPro, cf Sabbatini et al., 2018) which definitely requires a correction; secondly it clarifies the question of the cospectra transfer function shape and reconcile theory and observations. It also provides a new method to correct low pass filtering effects but I think that it’s robustness and applicability to routine measurements needs still to be proven.
For these reasons, I think that the paper deserves publication. As it is generally well written and structured, I think that only minor revision is required before acceptation.
I would add that this study comforts me in the opinion that, despite the great interest of theoretical studies that help understanding the causes and modalities of low pass filtering by eddy covariance systems, empirical approaches relying as little as possible on theoretical hypotheses remain the most robust ones to apply frequency corrections on routine measurements. In particular, in the present study, the approach deducing a transfer function from cospectra rather than from power spectra (Method 2) remains one of the most robust. The fact that the shape of the transfer function and the time constant are not exact is not very problematic to my opinion, as it does not affect critically the values of the correction factor, which is the target. The Method 4 proposed by the authours could be an interesting alternative, as it also relies on cospectra but uses a different transfer function shape. However, it is more complex as it requires the determination of two parameters (against one for Method 2) and, if the method worked well in the present case where the high frequency attenuation was artificially introduced, I suspect (and they confirm on P16L9) that disentangling the two time constants could be sometimes difficult, even impossible.
My regret is that the authors do not detail an implementation procedure of Method 4 for routine measurements.
Specific comments
The paper is the second of a series of two papers on spectral corrections. I was first asked to review the first of them (Aslan et al, also available on AMT discussions) but had to wait the submission of this one to really understand some issues and methodical choices of the Aslan paper. As the present paper appears to me more “standing alone”, I suggest to place this one in the first place and the Aslan paper in the second place. This is the order I followed for my reviews.
Introduction
The introduction offers a review of the knowledge about spectral corrections. It is clear and highlights the most important points. I have no specific comment about this except two small remarks :
P2L13: I think there’s a typo (“contribute” rather than “contributed”)
P3L7: Reference to Aubinet is not relevant I think as it refers to the chapter “night flux correction” in my book. I suggest to rather refer to the book itself or to a specific chapter (time lag is evoked in Ch 2 – Munger et al., 2012; Ch 3 – Rebmann et al., 2012 and Ch 4 – Foken et al., 2012).
Theory
I liked this chapter as it helps me to understand the issue of the cospectral transfer function shape. I must say honestly that I overlooked the debate about the presence or not of a square root in the cospectral transfer function shape (for my defense, I was more concerned in the past by the cospectral – Method 2  approach than by the spectral approach – Method 3) but, when comparing recently spectral and cospectral approaches on crop sites data, I found a better agreement when applying the square root (Method 3) than not (Method 1), which contradicted the theoretical predictions by Horst (1997), among others. I thus found the explanations given by this paper clever and convincing.
Two remarks, anyway:
P5L27P6L2: I don’t see the interest of presenting the approximation on L29. I tested the equation on L29 and found it fitted quite loosely equation 6. In addition, as I understand, this equation was not used in the paper and equality between tlpf and tau was not assumed further. Maybe could you consider to skip this.
P5L29: I’m wondering about the equality (and below, the proportionality) between tlpf and tau. Indeed, these two time constants are a priori not physically linked (except when both result from tube attenuation, which is of course an important case) and I’m wondering if you don’t loose generality by introducing this dependency. This question is discussed below but, in the end, there is no clear description on how you really implement the transfer function computation: do you fit an equation for H Hp based on equations (5) and (6) ? On equation (5) and those of P5L29? Do you consider tau and tlpf as independent parameters or do you relate them in some way?
Material and methods:
No specific comments. Clear and well presented. It is important to keep in mind (Sect 3.2.2) that the results presented below are not based on real measurements (I mean the attenuation is artificially provoked and does not reflect real attenuation processes), which is a limitation of the study (but this is well stated in the discussion).
Results:
P9L1324: Same remark as above: the proportionality between tau and tlps is clear here as both time constant result from an artificial attenuation but how would this relation look like in the case of measurements with a real attenuation and a real time lag, possibly independent ?
P9L2527: I was not sure to understand well: is it an approach that mimics the covariance maximisation procedure? If yes, it could be worth specifying it explicitly.
P10L2: What’s the meaning of s in Eq 14 (second, I suppose, but I would not mix symbols and units in a formula).
P10L34: This sentence let me hunger. As high attenuation could occur often (especially for gases other than CO2) this question should be clarified. Which attenuation levels do you consider? what is the order of magnitude of the bias? what is the impact of this bias on the next steps (correction factor estimation)?
P13 Fig 4: As I understand, the red curve corresponds to Method 1, the blue one to Method 3 and the black one to method 4. Is it correct? A direct reference to the method could facilitate figure reading (and why is method 2 absent from the figure?)
P14L5: isn’t it rather by the ratio of cospectral peak frequency to the cut off frequency ?
P15Fig6: The legend is not fully clear. I suppose that the symbols refer to the sites and the colours to stability conditions. This should be stated more clearly.
P15Fig6: I’m intrigued by the curve of Hyytialla in unstable conditions for methods 2, 3 and 4. Why is the bias positive, contrary to other site/conditions? Can you comment on this?
I’m also intrigued by the fact that the Method 4 more overestimates the correction factor than Methods 2 and 3 (and thus seems to work less good) at Hyytialla in unstable conditions. Here also I would expect a comment.
P15L26: I think that the figure shows clearly that the Method 1 gives different results from the three other methods. To my opinion Methods 2, 3, 4 provide all reasonable estimates of the correction factors while Method 1 biases the correction factors due, as you showed in the theory section, to a misinterpretation of the theory. In this sense, giving a relation to quantify the bias introduced by Method 1 is maybe not very useful. It could appear more clearly that this method is wrong and should be definitely not recommended (which notably implies a modification of the ICOS protocol).
P16L33: Same remark as above: don’t mix symbols and units in a formula.
P16L34: the meaning of x and y is not fully clear to me. Could you express the relation between these variables and time constants presented above?
P17L2, L5 and elsewhere: rather than referring to Section numbers, it would be more easy for the reader if you referred directly to the figures or tables presenting the results.
P17L7 and elsewhere: use a uniform notation to present the different methods (“Method X” is fine to me).
P17L9: one word is missing.
P17L10: As Hyytialla is equipped with a LI7200 and Siikaneva with a LI7000, I would have expected the inverse: a lower tau value at Hyytialla. Could you comment ?
P17L12 and foll: This section (and the legend of Table 3) should be clarified: In the text, are you presenting difference between correction factors? between half hourly fluxes? between cumulated fluxes? On which period? I finally supposed that you were comparing cumulated fluxes but this should be specified.
P17L12 and foll: I’m not convinced by the relevance of comparing relative differences on cumulated flux values. Indeed, relative values depend strongly on flux values (I suppose that H2O flux values at night should be low and in these conditions larger relative errors do not mean much). In addition, the low error on cumulated values may also result from partial compensation of errors (for example during day and night). I have the same problem when I try to compare different correction methods on my data set and I’m not sure to have the best solution. I prefer comparing the fluxes by looking at the slope between the fluxes submitted to different corrections. Anyway, in view of the preceding remarks, I’m not sure that the fact that Method 3 gives the biggest difference at both sites (L16) is really relevant.
P22L1; I feeled (of course!) concerned by the remark on our paper about the impact of dead volumes on the frequency response of gas sampling system. I could recognise that the fact that we didn’t distinguish physical time lag from attenuation induced time lag led to cut off frequencies that are probably not really representative of the attenuation. However, the general decrease of the cut off frequency with increasing dead volumes (our Figures 5 and 6) and the need for reducing these volumes in the gas sampling system were important results that we showed in this paper, along those of Metzger et al. And this again reinforces my opinion that transfer functions based on observed cospectra and taking thus account of all attenuation processes affecting the system (even if in some cases we do not fully understand all of them) are to be preferred for routinely correcting measurements, as they provide more robust estimates of fluxes.
Citation: https://doi.org/10.5194/amt2020479RC1  AC1: 'Reply on RC1', Olli Peltola, 09 Apr 2021

RC2: 'Comment on amt2020479', Johannes Laubach, 08 Feb 2021
General comments
This manuscript is a valuable contribution aiming to improve the data correction methods for eddycovariance (EC) measurements of trace gas fluxes. This is highly relevant because the EC method is used at hundreds of sites around the globe, often continuously for many years, to quantify the carbon exchange of vegetation, greenhouse gas source and sinks, and evaporation. The authors treat in detail, both theoretically and with experimental data, how the effects of highfrequency attenuation of gas measurements and of time lags between the gas and wind measurements influence and compound each other. With that, they clear up two points of debate and sometimes confusion (see below) and give guidance how EC gas flux computation algorithms should be organised. Given the widespread use of EC for gas flux measurements, this paper has potential for high citation count.
(1) The first point of the debate clarified here is that, with correctly determined physical lag time between wind and gas (or other scalar) signals, the transfer function for cospectral attenuation is equal to that for the scalar's power spectrum, not to its square root. Even though this has been shown in detail before (Horst 1997), it is worth stating again because the erroneous square root keeps appearing in recent eddy covariance methodology papers, such as Nemitz et al. (2018).
(2) The second point is novel and shows how things change if lag times between wind and scalar signals are determined using covariance maximisation (with uncorrected attenuated data). The covariance maximisation is a dubious yet widespread practice. It overestimates the lag time by including the phase shift effect of the lowpass filtering. The authors show that after covariance maximisation, the cospectral transfer function is no longer equal to that derived from the power spectrum, and they derive a correction to compensate for this. This correction is the truly novel contribution of this paper.
Unfortunately, (2) gets a bit muddled up by the authors claiming that the cospectral transfer function after covariance maximisation is obtained approximately if the square root of the power spectrum's transfer function is used to correct the cospectrum, i.e. by reverting to the original misconception addressed in (1). In other words, one imperfect (or incorrect) processing step would be fortuitously compensated by another. I strongly suggest refraining from putting it this way, because a) in a mathematically exact sense, it is incorrect, and b) the approximation will quickly become inaccurate for lag times exceeding 1 second (outside the range tested in this paper). I explain these reservations further in the Specific Comments.
Overall, I think this manuscript is worthwhile publishing after revision (as detailed below) and with modified conclusions, along the following lines.
In my view, there should be a strong recommendation to discourage usage of the covariance maximisation method in the future. It is known (and nicely illustrated here) to be incorrect, by mixing two separate effects. In addition, it produces erratic unphysical results when fluxes are close to the detection limit (affecting typically most nighttime periods for H2O and the morning/evening transition periods for CO2).
It is not that difficult to determine the physical lag time with other methods. Firstly, its expected value can be constrained by geometrical dimensions of tube and measurement cell, together with pressure and flow rate (which is known or even controlled for many gas analysers, and if not, a flow meter can be added). Lags due to clock mismatches or processing delays need to be included, too. Once the expected lag time is estimated in this way, it can be empirically confirmed (e.g. by popping a balloon filled with synthetic air next to the sonic anemometer and the air intake). Alternatively, the lag time can be determined AFTER obtaining the transfer function for the gas power spectrum and applying the corresponding lowpass filter to produce a degraded temperature spectrum: the correct lag time should be that which maximises the crosscorrelation between the degraded temperature time series and the gas time series.
Determining the lag time with any of these methods, followed by the correct cospectral correction (1), should be the preferred procedure.It is understandable that the authors wish to promote their novel correction, and I concede that it may be useful in some cases, especially where lag time determination with other methods is difficult or not possible any more (historical data). A modified conclusion to that effect would be acceptable.
However, the authors should not recommend reverting, after covariance maximisation, to using the square root of the powerspectral transfer function. That approach reminds me of the Copernican approach of retaining epicycles in the planetary orbits, in order to rescue the tenet of circular motion: a physically wrong and complicated correction of a calculation procedure that is necessary only because the original procedure is based on a flawed assumption. It may be reasonably accurate (as for the data used here) but nonetheless should be abandoned.

Specific comments
Introduction and Theory as far as P 5 L 18 are very well written and I fully agree with the content. One minor point:
In P 3 L 22, the "^" notation is introduced prematurely and should be removed. Its introduction is repeated in P 4 L 15, and it is not used in any numbered equation until (9).P 5 L 2032
I contend that the statement "Co_m can be approximated by A_m" (L 2021) is wrong. Covariance maximisation delivers a lag time t_used which differs from the true t_phys. The mathematical treatment to describe how the time series of w and X shifted by t_used combine with each other is completely analogous to Eqs (2) to (4) with phi_used replacing phi_phys. Eq (4) shows how there is always a frequencydependent shifting of amplitude between Co_m and Q_m. In other words, it is not possible to make Q_m disappear for all f simultaneously. Hence, while Eq (10) is the correct result for A_m, it is incorrect to equate A_m with maximised Co_m. In fact, your statement on P 12 L 35 shows that you are aware of this, hence the text here should be revised to reflect that.
The paragraph starting in L 27 describes your procedure for estimating H_p. It does not stop with assuming H_p = 1/sqrt(H). This is actually the novel part of the Theory section, and it should be written out with numbered equations and clearly stated approximations, ending with the equation for H_p that you are using in practice (e.g. Fig. 4).P 6 top
In my view, the Theory section should not end here yet because you did actually take the analysis further, in Sections 4.14.2. It should at least be anticipated here that empirical analysis was used to get a better estimate of H_p.P 8 L 1518 Two comments: Firstly, "Method 1... is implemented e.g. in EddyPro after Hunt et al. (2016)": this is incorrect. The method CAN be implemented there, but does not have to. The user is free to choose which lag time determination is used, and Hunt et al. used a fixed lag time.
Secondly, if EddyPro is mentioned here, then it would be worthwhile clarifying that older versions implemented the "sqrt(H)" transfer function, while later versions implement the correct "H" transfer function. The change was made as a consequence of correspondence between Laubach (Hunt's coauthor) and Fratini, as explained in a footnote of Hunt et al. (2016). So, for carrying out Method 3 with EddyPro, users would need to employ an older version.P 8 L 1920 "Throughout the study, crosscovariance maximisation was used...": that means that later when assessing CO2 and H2O flux data, no true reference (with correct lag time) is available  which is a pity!
"... as typically done...": I would be curious to know how widespread this practice really is (given the practical problems with small fluxes, when estimated lag times can be all over the place). Of course that is outside the scope of this paper. I'd just like to caution the authors that not every EC user does follow this practice, and as noted above, the EddyPro software offers alternative choices.P 9ff
I find Section 4.1 very hard to follow. First, C is frequencydependent (Fig. 1 top), then it is set constant without clear motivation (Fig. 1 bottom), then windspeed dependent (Fig. 2). Is it possible to rewrite this section to be less adhoc and with more rigour, and perhaps put relevant equations at the end of the Theory section (with a note that empirical coefficients will be determined in the Results)?P 11 L 11 "as is typically done": cautionary note that this is an assumption about other users (as for P 8 already). Figure 3 is a very convincing illustration why the covariancemaximisation practice should be abandoned, and I'd love to see a statement to that effect!
P 12 L 25
"Q_m cannot be nullified": here the authors agree with my earlier comment. The sentence in L 35 should be moved to the Theory, below Eq (10).
"H H_p not exactly equal to sqrt(H)": in fact, the appearance of negative values means that the two expressions are fundamentally incompatible. As Fig. (4) shows, increasing the time lag has the effect of shifting the negative region towards lower frequencies, where it causes greater flux losses. The approximation as sqrt(H) then becomes inadequate quite quickly, with big effects in practice for "sticky" gases like H2O and NH3, where tau can easily exceed 1 second.
Since you actually have a method to compute H_p, with results shown in Fig. 4, I do not understand why you keep repeating the point about (inaccurate) resemblence to sqrt(H).P 13 L 1 "somewhat underestimated CF": better quantify (about 5 %?)
P 13 L 910, Fig. 5: I do not find Fig. 5c useful. The dependence of t_lpf on tau has been extensively covered in Section 4.1.
P 14, Table 2: How come that Methods 2 and 3 have relative differences of order +/1 % when Fig. 5a suggests correction factors about 5 % below the reference? Does that mean the largest fluxes systematically had the smallest corrections? Does the extended dataset behave differently to the smaller sample underlying Fig. 5? Some explanation of this is needed.
P 15, Fig. 6: Why does Hyytiälä not show any negative values for Methods 2 and 3? Was the chosen tau range too small to simulate noticeable flux losses?
P 1718
Figs 7 and 8 are interesting. Unfortunately, as stated before, there is no true reference available because t_phys was not determined with any other method than covariance maximisation.
It may be useful in these figures (and perhaps already in Fig 4, too) to show some averaged or typical cospectrum in a second panel above or below the transfer functions, to give the reader an idea which cospectral regions were affected by the lowpass filtering. It seems that with the data used here it was a relatively minor part, hence flux losses were generally small. While this situation is highly desirable (meaning the experimental setup was nearoptimal), it is not always achievable, and a different dataset with greater flux losses may lead to comparison statistics quite different to those in Tables 2 and 3. The last few lines on P 18 already hint towards that; perhaps make this discussion point a little bit stronger. This suggestion is based on my own experience at agricultural sites with mast height restrictions (2 m) to allow for irrigators moving overhead. There, particularly for H2O the flux corrections can be substantial, of order 30 to 50 %, in which case the correct shape of the transfer functions matters a lot more than in your datasets.P 2022:
It would help the reader if the "Summary and Conclusions" section was shortened greatly, to "Conclusions" only, with clear recommendations on future data processing (less is more!).
Of the listed conclusions, the first should end with a recommendation to abandon the covariance maximisation method wherever possible (P 20 L 31).
The second (P 21 top) should be shortened to its first 3andahalf lines ("... caused by covariance maximisation"). The statement that "(H H_p) can be approximated with sqrt(H)" should be removed because it becomes highly questionable when the negative region of the transfer function reaches into lower, fluxcarrying, frequencies. The content of L 59 is unnecessary repetition of points made in Section 4.4.
The third (P 21 L 1017) does not lead to a clear recommendation (other than reinforcing that covariance maximisation is best avoided), so I suggest removing. The fourth (L 1822) only repeats the second, remove. Instead, consider adding a recommendation to check whether past Fluxnet datasets have been processed with a consistent method combination for determining lag time and transfer functions. Where an erroneous mix has been applied, the data should be reprocessed. A statement on the expected fractional changes from such reprocessing could be added (based on your Results, but somewhat speculatively with respect to other EC setups).
The last conclusion (L 23 to end) could be condensed and rephrased as an "outlook" towards which other aspects of cospectral corrections require further investigation.
Minor technical comments
P 2 L 10 "trough" should be "through" (before "tubes")
P 2 L 1519 (and possibly later): For easy reading, I suggest using one of the pairs "lowpass"/"highpass" and "highfrequency/lowfrequency", but not mixing the two.
P 6 L 11 & 12 It is usual practice to give town/city of the manufacturer, too, not just the country.
P 6 L 17 remove hyphen between "Sphagnum" and "species".
P 6 L 18 replace "with the height" with "with a height".
P 8 L 6 insert "to" between "prior" and "utilising".
P 18 Table 3 caption: "was used" should be "were used".
Citation: https://doi.org/10.5194/amt2020479RC2  AC2: 'Reply on RC2', Olli Peltola, 09 Apr 2021

RC3: 'Comment on amt2020479', Anonymous Referee #3, 15 Feb 2021
General comments:
This manuscript discusses Eddy Covariance (EC) flux postprocessing corrections. They present important clarifications to the theory and demonstrate the presence of a systematic bias in some standard postprocessing software packages from time lags induced by lowpass filters in closed path EC systems when using the crosscovariance maximization technique to determine lag times. They also present a correction method to account for this effect and provide a thorough theoretical and empirical discussion of its implementation. This manuscript is well written, and the topic is well suited for AMT. The methods presented here are likely to prompt reprocessing of a number of historical flux data sets and the revision of some of recommended best practices for EC flux processing. I recommend publication after some revisions.
Specific Comments:
P5 L27L32: The equations presented here are quite important and should be broken out into numbered equations.
P6 L21: What is the calculated transit time through the sampling tube from the volume and flow rate (if that information is available).
P9 L310: The limitations at higher attenuation levels needs further comment. Long responses times are common for studies of more reactive trace gases and it is not clear if this method should be considered in those cases. Some explicit guidelines for the reader about where this method breaks down would be useful.
P12 L13: This inequality seems important and draws into question the utility of approximating to sqrt(H) when you present a method to calculate H H_{p}
P14 L8: Why does the bias in CF only increase linearly with τ/ITS at Siikaneva and not Hyytiälä?
P15 Fig6: It is interesting that the Hyytiälä data for unstable conditions shows a positive slope for Methods 24. Some discussion of this would be useful.
P16 L4: Calculated t(phys) from tube volume and flow rate would be helpful here as well if that information is available.
P17 L17: Further comment on this discrepancy is needed. Is the implication that the response times were fast enough that the LPF induced lag time was minor compared to other potential factors?
P20 Summary and conclusions: It is addressed in the third point but I think it is warranted to be more direct in discouraging the use of Method 1 based on your clear demonstration of systematic biases using that method.
Misc: The use of crosscovariance moving average methods for determining lag times (as in Taipale et al. 2010) is becoming more common as an alternative to the crosscovariance maximisation. The attenuation induced lag time effect and your Method 4 correction should be equally valid when this method is used, but a brief comment would be useful.
Minor Technical Comments:
P8 L6: insert word “to” after “prior”
Figure 3. Recommend making the colors more distinguishable.
Figure 5 panel b. Why is Method 1 not plotted
P16 L10: Wording of this sentence is unclear “can attain values only with the temporal resolution of the underlying data itself”.
References:
Taipale, R., Ruuskanen, T. M., and Rinne, J.: Lag time determination in DEC measurements with PTRMS, Atmos. Meas. Tech., 3, 853–862, https://doi.org/10.5194/amt38532010, 2010.
Citation: https://doi.org/10.5194/amt2020479RC3  AC3: 'Reply on RC3', Olli Peltola, 09 Apr 2021