I recommend considering the manuscript for publication in AMT after major revision.
Major comment:
Although already suggested in the first reviews, the author's work has not yet been put in the right scientific context. Turbulence and heat flux measurements from rotary wing UAS are indeed a fairly new topic, and the novel approach presented in this study is very promising. However, at least one important article (Ghirardelli, et al. 2024) is not cited, although this is, to my knowledge,e
the first time the EC method has been applied in combination with a rotary-wing UAS and validated against mast-mounted ECs. Although, already suggested to include in my previous review. All relevant approaches for multirotor-based flux measurements deserve to be presented, and the proposed approach should be contrasted against the existing ones. Using a small UAS certainly has some advantages over larger systems, but it is likely to also have some disadvantages.
The fact that the separation distance impacts the comparability needs to be addressed more adequately. Comparing raw time series or time-averaged data from several different locations in rather non-stationary conditions is challenging. E.g. a good correlation can only be expected when the time lag between two time series is much shorter than the "non-stationarity time scale". At least it has to be discussed how this impacts the results, that even if all systems capture turbulence perfectly, the proximity of the UAVs to one of the masts is expected to yield higher agreement compared to the two masts standing roughly twice as far apart. A time lag correction based on cross-correlation or based on mean wind speed and separation in the along-wind direction would reduce this problem, although the problem of non-coherent smaller-scale turbulence would remain.
Specific comments:
Title: I don't see why "sensible heat flux" has been changed to "heat flux". Maybe this is related to my previous comment on the difference between buoyancy vs. sensible heat flux, but the proposed method is suitable for measuring the sensible heat flux, so I suggest sticking to this.
Abstract:
L8-9: I still disagree with the statement that this is the first time sensible heat fluxes have been measured (accurately) using multicopter UAS. My previous comment on this has only been partially addressed by including two suggested citations (i.e., Fuertes et al. 2019; Greene et al. 2020). However, Ghirardelli, et al. (2024) is not cited, although this is to my knowledge the first time the EC method has been applied in combination with a rotary-wing UAS (in this case, measuring the buoyancy flux using a full-scale sonic anemometer). As mentioned, I agree that this is the first time the sensible heat flux has been measured with the specific method presented in this manuscript or, more generally, applying the EC method from small UAS, but the current statement simply ignores the work done by Ghirardelli, et. al. (2024). Given the rather high discrepancies compared to the sonic anemometers, the accuracy of the measured fluxes should be put into better perspective since the uncertainty is still rather high (also for the experimental setup).
L11: I suggest simply stating the wind speed range. Furthermore, I consider 8 m/s as rather moderate wind speed and given that the minimum wind speed listed in Table 2 is 2.9 m/s, the term "low wind speed" doesn't describe the range of conditions very well.
Introduction
L30: The new statement, "Another alternative is to put sonic anemometers on UAS? with the drawback of requiring much larger systems." should probably refer to Ghirardelli et al. (2023) and Thielicke et al. (2021). The cited articles are not visible and don't show up in the bibliography. The study Ghirardelli, et al. (2024), presenting a xUAS with a sonic anemometer in a sling-load configuration, is in this case more relevant than Ghirardelli, et al. (2023), which illustrates the feasibility of using sonic anemometers on xUAS based on CFD simulations. Furthermore, "larger systems" also have their advantages, e.g., longer flight times and the capability to carry more sophisticated sensors, to name a few highly relevant advantages of this approach.
L38: Start a new paragraph
L31-L32: The statement is still kept too general and thus misleading. When considering a dedicated flow sensor, the separation distance between the sensor and the rotors, as well as the mechanical implementation, are important parameters. Furthermore, the sensor specifications e.g. size and sampling frequency, determine the smallest resolvable scales. For this reason, it would make sense to limit the statement to the specific sampling approach.
Figure 2: Please correct the caption of Figure 2 (red circles).
Table 1: The Table has been improved a lot, and together with Table A1, it gives a clearer overview of which UAS have been used. However, I still lack a more detailed caption, allowing the reader to understand more easily what the different columns indicate. Some basic details on the source of the listed background conditions should also be provided here.
L156-L157: This is the definition of the sonic temperature so "...which is often referred to the 'sonic temperature'..." should better be changed to "..., the sonic temperature, ... "
Eq. 2: Please remove the +273.15K in the equation. Conversion from sonic to air temperature works fine when using either units (K or degC) consistently. The equation in its current form only works for T in degC and Ts in K.
L161: Use "sonic temperature" instead of "equivalent sonic temperature".
Fig 3: According to the authors' response, this figure should have been removed.
L169-L170: This new statement is still slightly misleading. The following should be corrected:
- The bouyancy flux is proportional to cov(Tv'w')
- cov(Ts'w') is a good approximation for the kinematic vertical flux of virtual temperature cov(Tv'w'), but requires scaling with density and specific heat capacity to yield the buoyancy flux
- Eq. 6 should be kept as is, but should indicate that this is the approximation applied in this study to estimate the buoyancy flux from the sonic anemometer data. Furthermore, it should be made clear that you compare the sensible heat flux from your UAS to the buoyancy flux from the sonic anemometers and provide some estimate on the difference between these two under the prevailing conditions. When would the contribution of the latent heat to the buoyancy flux become problematic?
L205-L210: This section would benefit from some cross-references to the relevant equations. E.g., I assume that a 0D calibration would result in c1 in Eq 7. being a certain constant.
Table C1: This table shows only 13 out of 25 sensors. Are the other 12 sensors 0D calibrated or not used at all? Does n.a. indicate that standard coefficients c0 and c1 are being used? I would assume that they can't be completely unknown since they are needed for the conversion from R to T. Delta T should not be given with varying precision. In the current form, a Delta T = 0 suggests that the bias of most sensors is below 0.00K, which is a bit hard to believe. Please also indicate your findings on the long-term stability (sensors 1 and 4) in section 4.4. The unit of c0 should be indicated (degC).
Sect 4.5.: It is very helpful to have this section; however, in its current form, it is not clear how the different parameters are determined: the gravitation and acceleration term in Eq 8 can be easily determined from INS data, but it is not clear how T and FL are determined. In Eq9 and Eq10 it is not clear what c is and how it is determined, and why two different cases are treated depending on the sign of Fz. Are the coefficients c identical for the body frame and geodetic coordinate system? From a purely physical consideration, calculating a velocity from a balance of forces requires some integration in time. I assume that this is somehow accounted for by the coefficient c. However, this leaves me wondering about the initial conditions required for the integration and the sensitivity to sensor drift. I assume that small errors in the INS data would add up over time.
Sect. 5.2: Fig 7a shows four Fig 7b shows five UAS. Please adjust the text and caption accordingly, also indicating that you now show two calibration flights.
I think the correction is described in Sect 4.2 and according to this and Fig 7 you convert the UAV temperature to sonic temperature (not virtual temperature). The deviations between the sonic and UAV data, and also between individual UAV data, could also originate from errors in the HYT humidity readings.
L249: "mean absolute deviations" instead of "average relative deviations"
L264-L266: Can you provide an equation or a reference for the time-lag correction? I recommend to state that 20s is much longer than the stated time constant (HYT-271: <5s, HYT-R4211: <2s)
Table 3: Please use the same precision (number of digits) for all numeric results of the same parameter to allow for a proper comparison (not only in this table).
L305: add reference to Figure 10a. In general, it is a bit strange to start with Fig 10b. I would recommend to briefly introduce Figure 10 in a more general way.
L306: should be "slightly higher"
L317: put citation in parentheses
L325: Figure 11 has been improved by also filtering out values not fitting the UAS criteria in the sonic-sonic comparison. However, it still looks like there are some differences. It is hard to count the unmasked data points, but it still looks like there are quite a few more in 11 a than in 11 b although n is almost equal. I also still have difficulties finding some distinctive data points in 11a e.g. for H > 400 W m-2, there are two data points in Fig. 11b but no such point in Fig 11a. If 11a should serve as a benchmark for the experiment uncertainty, I expect this to be based on the same data points as in 11b. This means the number of data points should be identical as well as the sonic heat flux values in 11b should be found either on the south or north mast in 11 a. Since the conclusion from this analysis is that the UAS-based flux measurements fall within the experimental uncertainty, it is important that this uncertainty is benchmarked as correct as possible. The argumentation in the author's reply to my previous comments (reply 50.) that strong temporal variability is often observed, resulting in very different fluxes when shifting the start and end of the averaging intervals, leaves me wondering whether different averaging intervals have been chosen. If it is the case that the averaging intervals are different, this should be mentioned to put the results in the right context, although I would prefer to see this corrected. Given the mentioned temporal variability (as shown in Figure 12), I would still advise correcting the time lag expected for the separation distance, and prevailing wind speed and direction or at least provide a proper discussion that some of the discrepancies between the two masts can be attributed to the roughly twice as long separation distance.
L339-L343: mention that QAV15 and QAV25 are next to the southern mast. It is not clear that the right panels in Fig 12 correspond to the 99m level UAS and sonics. Please also indicate this in the text and the caption. Please also explain what the shaded areas and error bars are based on (also in the caption).
L354: How do you get to the value of 1 m for the turbulent scales that can be resolved? Would it be more accurate to state the temporal resolution of 2 Hz, since this is supported by your spectral analyses?
Conclusion:
Flights 69 and 70 (Table 3) only partially support the claim that turbulence can be measured accurately. |
The manuscript "Towards sensible heat flux measurements with fast-response fine-wire platinum resistance thermometers on small multicopter uncrewed aerial systems" by Norman Wildmann and Laszlo Györy is well within the scope of AMT, presenting a novel method to measure the sensible heat flux by combining fast-response temperature measurements from a platinum fine wire temperature sensor and vertical velocity estimates retrieved from the UAS flight state data. While the authors carry out an extensive validation of their new measurement approach against a well-established reference system and also take the expected uncertainty of the experiment into consideration, the methods presented and used in this manuscript may not always be the optimal choice. Furthermore, the level of detail in the documentation of the methods and the scientific background is not always high enough. To put the manuscript in the correct scientific context it also lacks a few references. I therefore recommend major revisions before considering the manuscript for publication in AMT.
- Table 2:
- Are the names related to a specific model version? If yes, the differences should be described; otherwise, this column is rather irrelevant and could be dropped.
- How is delta Ts computed?
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