Haghighi et al. present an exciting new measurement system that allows to sample the atmosphere up to 25 km with high resolution. It is great to see that the authors could perform these measurements and that they could measure exciting features in the atmosphere. I have some concerns about data processing and analyses which need to be revised before I can recommend the manuscript to be published in AMT.

General comments:

- I do not trust the Ri-number calculations which are presented. The oscillations that can be seen in the vertical profile seem unrealistic and I have a strong suspicion that the error starts with the wind measurement, as described below in the specific comments. Please check and make sure that the wind measurements are not heading-dependent and estimate the uncertainties for your system.

- The title and the abstract suggest a deeper analysis of the infrasound measurements, the error sources and the uncertainties, but the manuscript leaves me with the impression that these measurements can not really be used because it is often unclear where the detected signals originate from and how to process / correct them. It would be good to at least show a path forward for this.

- The gravity wave analyses are very nice. The polar plots give some insight, but it would be easy to analyse the origin of the waves better when some model data is included and 2D maps of the wave structure at different altitudes was shown. I encourage the authors to consider that to make their very vague and speculative statements more robust.

Specific comments:

p.8, l.192: was the attenuation of the probing also verified by experiment? what can you read from the spectra?

p.8, l.195f: if this data is shown, you need to explain the method in more detail.

p.11, l.253: Where do these 10% come from? What do they even mean? It does not look like there is a relative error below 10% for wind speed and wind direction at all times. I would not expect it, given the temporal and spatial separation, but the value should be explained.

p.14, Fig.7: The periodicity in the Ri-number with height is very suspicious. Looking at Fig.4 I get the feeling that this could be caused by flight direction. It is known that wind estimatino from multi-hole probes on fixed-wind aircraft is very sensitive to heading estimation. Please show the dependency of your wind measurements to heading. I think the periodicity already shows in wind speed and wind direction measurements. I doubt that the Ri-number calculations are meaningful with this uncertainty in the wind estimation. It should be qualified with an uncertainty estimation.

p.18, l.341: how were the thresholds for $n$ chosen here?

p.18, l.362: so, if I understand this correctly, in a circular flight, the horizontal flight direction changes all the time and thus does the wind vector component you are using for EDR estimation. I think it would be more reasonable to align the rotated wind vector to the mean wind direction. $u$ and $v$ are not expected to show the same spectral characteristics. In a circular flight you are also distorting the measurement, even if the Taylor hypothesis is valid. Maybe the radius is so large that within 30 seconds, the curvature can be neglected, but you should reflect on this.

p.20, l.414: This is a bit misleading. You did not add horizontal flight legs at these altitudes, it is still the same flight pattern, spiraling down, right?

p.21, l.428ff: These are quite interesting observations. It would help to show the temperature and velocity fluctuations for distinct altitudes on a horizontal (map) plot.

p.21, l.429: How do you determine the wavelength?

p.22, Fig.12: The shaded region is Ri>1 or Ri<1? It is not clear from the caption

p.25, l.465: you mean figures 12 d and e, right?

Figs. 12, 13, 14: The variable names and units should be given in the plot itself, not only in the caption.

p.27, l.534: I would highly recommend to obtain some reanalysis data from NWP models (e.g. ERA5) to see if conditions were favourable for gravity waves and if they can be seen in the model. This could be nicely added in an appendix.

Technical corrections:

p.1, l.3: "thermodaynamic"

p.3, l.61: "from with"

p.7, l143f: two times "changes with the horizontal axis" should probably be vertical axis the second time.

p.8, Eq.4: $dir$ is not a proper variable symbol.

p.8, l.194: disconnected disconnected

This paper presents some intriguing results using a new measurement platform for profiling the atmospheric column descending from about 20km. However, the quality of the observed data is not clear, given the periodic variations that may be a result of the periodic orbit of the gliding aircraft platform.  As a result, the conclusions drawn about the viability of the sensing method and the relation to potential atmospheric structures and sources is tenuous, without furhter examination of the correlations between signal variations and platform motions.

Detailed comments:

• Introduction: “The trajectory of the glider allowed for improved statistical convergence and higher spatial resolution of derived statistics measured by the in-situ sensors.” Refers to balloon-borne measurements, but such improvements and higher spatial resolution were not demonstrated in the paper.
• Similarly: “which allowed the connection to be made between the locations of increased turbulence intensity and the source of its generation” was tenuous, only to the level of “consistent with”.
• 40: “with these results used to model the relationship between turbulence in the stratosphere as well as tropospheric activity” not clear: “as well as” vs. “and”?
• 85 “However, due to the transient nature of their Lagrangian flight trajectory, balloon-based approaches are not necessarily amenable to obtaining detailed statistical descriptions of turbulence at high altitudes.” Why? Aircraft are also transient, and if GPS guided, only see what is advected past. Balloons with altitude profiling are not Lagrangian vertically, so also sample more than one parcel of air. The statement is vague: it depends what statistics are being evaluated.
• 90: “A glider offers advantages over traditional balloon launches by being able to maximize time at altitude during its descent phase” Vertical rates for the glider vary from 5m/s to 1 m/s, very similar to descending balloons. “These qualities facilitate the statistical analysis necessary for quantification of non-stationary properties” is not supported by evidence in the paper.
• Difficulty of conducting UAS measurements of this type in the NAS was not discussed, nor the conditions under which the reported flights were allowed. Was this in restricted airspace? Under who’s auspices? Or was this in the NAS under a COA?
• 125: The iMET sensor specifications were not referenced. These accuracies and time constants tend to degrade at lower pressures and temperatures, and this was not indicated.
• Figure 3 would benefit from the addition of dimensions to the components pictured.
• 150: “Comparison of calibrations with and without heating active indicated that there was no influence of probe heating on the five-hole-probe response characteristics.”  Not clear what response characteristics means: time constant? Calibration coefficients? Noise level?
• 153: “Each hole on the probe was connected to differential pressure transducers through 1.75 mm diameter flexible polymer tubing.” What was the other port of the differential pressure sensor connected to? Presumably this was the “static pressure port”, but this was not shown or described in the paper. How long was the tubing (this can have a detrimental effect frequency response of the air speed measurement, as noted later in the paper).
• 160: “Note that the during flight, the autopilot maintained flight speeds sufficient to produce pressure differences well within the range of the low-sensitivity transducers and hence only the readings from these sensors were used for this analysis.” Please quantify the airspeeds obtained, and the corresponding average differential pressures.
• 195: how was aircraft sideslip angle determined? How did the use of this affect the quality of the horizontal wind measurements?
• Generally, the details of this particular mutli-hole probe and its calibration and resulting accuracy were not provided. Can these be referenced from an earlier publication?
• 205: How was the microphone mounted on the vehicle? Was it protected from dynamic pressure fluctuations? If so, how did this filter the infrasound pressure waves? Could aircraft motions (that are also dependent on ambient turbulence) influence these measurements?
• How are winds calculated?
• How is airspeed calculated? No plots of airspeed were provided. What was the airspeed as a function of altitude?
• 220: temporal alignment can be intricate. How was this accomplished with this data? Was there a common time reference?
• 230: what does “controlled landing” mean here? Manual landing (RC), or automatic landing (autopilot)?
• 229: A portion of the descent from the 30km release seems to be very steep. There were also some very tight circles at isolated po Due to the configuration of the sensors on the aircraftints in the first two descents. Why?
• 235: I think you mean UTC -6:00 here.
• 239: “Due to the configuration of the sensors on the aircraft”. Vague. Please describe what about the configuration makes the sensor readings unreliable on ascent.
• 289: “with backing”?
• 295: central differencing between adjacent 30 sec averaged values?
• 230: regression fit to a constant function over 150 sec? Central 30 sec interval with 2 intervals before and 2 after?
• 271: “this is likely due to spatial heterogeneity in the atmospheric moisture concentration”. Could also be due to an instrumentation anomaly.  The following statement  “cloud conditions near Truth or Consequences, NM (near Spaceport America) were different” does not help. Different how? At what altitudes?

• 276: compare well given the spatial offset and the local weather conditions, and if the local periodic variations are ignored. These variations are suspiciously periodic with altitude, raising questions about artifacts from the platform airspeed/attitude/descent rate that may be varying with the same period. (See the related comments about Ri later). Some evidence should be provided that these results are not correlated with aircraft motions.
• 300: Although it probably does not make much difference, z in this formula should be altitude MSL, not AGL. Recommend that MSL be used throughout for consistency and for interpretation of the results. Also, I can’t seem to find the altitude of the ground at the launch location.
• 303: The Ri profiles seem to have highly periodic excursions with altitude. Could these be at the same period as the orbits the plane executes on the descent? That is, how do we know this is not an artifact of the sensors or the periodic motion of the platform? It would also be good to see how this correlates with the bank angle of the plane, since this will not be constant in wind. It will be difficult to take the results at face value without careful checking for motion/attitude/descent rate artifacts from the platform. Similarly, the Ri values seem suspiciously low, with < 0.25 values for much of the flight. Are these low values periodic anomalies in the measurements?
• 323: how does <u> differ from <U> used earlier?
• 327: what were the subintervals and overlap used in the Welch method? The “spectra” in Figure 8 seem to have a 40s period fundamental frequency, so this is confusing.
• F_uu and Phi_uu are both used for the power spectral density (please be consistent), and these are incorrectly called the “frequency spectrum”.
• 328: Was the Hanning window variance-preserving?
• 329: integration of the PSD is from .025 Hz to 5Hz, so the most important (largest amplitude) components of TKE are potentially not included. This makes TKE difficult to estimate without some idea of the local “outer scale” where the spectral energy ceases to increase as frequency decreases. This is noted later (347), but with a confusing reference to 300m as the longest period in the k “measurement”, since earlier in the paper 2420m was quoted as the longest interval in the 30s analysis intervals.  However, no mention of the outer scale was made. Thus the k retrieval has a highly variable lower spatial scale with altitude, and the relevance of the k profiles is unclear.
• 339: shape of the “spectra” in Figure 8 is very strange. Part a) seems to have a noise floor near 10^(-3), but the noise floor is smaller (near 10^(-6) at a higher altitude (part b)! (Where pressure fluctuations are necessarily smaller). A noise floor is again seen near 10^(-3) in part c). Also, the spectral slope is too shallow in part c) as noted later in the paper. Could it be that this power spectral density is the noise figure of the sensor itself, and there is really no detectable signal at these low atmospheric pressures?
• 356: Buoyancy Reynolds number can be calculated after estimating epsilon, as a check on this assumption.
• 364: the kappa_1 wavenumber component in (9) is the longitudinal component of the motion of the air relative to the sensor. This is only the longitudinal component of the vehicle ground velocity in the special case of zero mean wind (still air), or in the limit when the vehicle airspeed is much larger than the wind speed. This should be corrected to use the airspeed, and the course heading frame rotation should be replaced by one based on angle of attack and sideslip of the sensor relative to the relative wind vector.
• 366: again use of ground speed here in incorrect. Must be airspeed.
• 367: I don’t understand the expression for Phi(kappa_1).
• Figure 9: Suggest plotting k and epsilon (or EDR) on a log scale to look for periodic artifacts (as noted earlier), and to make it easier to see the full range of these power function values.
• Not clear how (of if) the noise floor/noise figure is removed in the qualified data fits.
• 386: “It will be shown later that this enhanced EDR corresponds to measured
• fluctuations in velocity introduced by the presence of gravity waves at these altitudes”. How? Gravity waves have a much large wavelength than could be influencing these epsilon estimates.
• 401: confirmation that the infrasound signal is due to turbulence is too strong a conclusion at this stage. Localized increases do not correspond to those in EDR.
• 426: the “interesting features” in figures 12-14 show strong correlation with location on the flight path circle. This might be due to differences in structure in the atmosphere across the 5km circle diameter, but it might also be due to sensor signal dependence on the heading or attitude or airspeed of the vehicle, that is also periodic with location on the flight path (as noted above). Given that these “features” in the data persist over large altitude ranges (where e.g. shear and stability are expected to vary significantly), and the intermittent, sometimes contradictory correlations noted in the paper, it is difficult to consider the conclusions offered as more than optimistic interpretations of rather murky relationships. Too much is made of data that has not been thoroughly vetted.
• 449: Ri is used as a marker for stability in various places, which is confusing. Stability is indicated by N. Ri combines N with horizontal shear.
• 441: an “identification” the source of observed EDR here is optimistic here, given the weakness of the “suggestions” seen in the data. Again, “wave” activity may be due to measurement anomalies that are periodic with vehicle motion.
• 451: given the strong horizontal advection, it is difficult to believe that turbulence features originating in the boundary layer could propagate into the stratosphere within the short 5km diameter of the (inertially fixed) helix of measurements.