Long-term lidar observations of the gravity wave activity near the mesopause at Arecibo

Yue, Xianchang; Friedman, Jonathan S.; Zhou, Qihou; Wu, Xiongbin; Lautenbach, Jens

doi:https://doi.org/10.5194/acp-19-3207-2019

Articles | Volume 19, issue 5

https://doi.org/10.5194/acp-19-3207-2019

© Author(s) 2019. This work is distributed under
the Creative Commons Attribution 4.0 License.

Special issue:

Layered phenomena in the mesopause region (ACP/AMT inter-journal...

https://doi.org/10.5194/acp-19-3207-2019

© Author(s) 2019. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 19, issue 5

Research article

|

12 Mar 2019

Research article |

| 12 Mar 2019

Long-term lidar observations of the gravity wave activity near the mesopause at Arecibo

Xianchang Yue, Jonathan S. Friedman, Qihou Zhou, Xiongbin Wu, and Jens Lautenbach

Download

Final revised paper (published on 12 Mar 2019)
Preprint (discussion started on 26 Jul 2018)

Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

- Printer-friendly version

- Supplement

RC1: 'Review of Long-term Lidar Observations of the Gravity Wave Activity near the Mesopause at Arecibo', Anonymous Referee #1, 30 Aug 2018
- AC1: 'Response to the Referee #1', Xianchang Yue, 23 Sep 2018
RC2: 'Review of Xianchang Yue et al., Long-term lidar observations of ...', Anonymous Referee #2, 14 Sep 2018
- AC2: 'Response to the Referee #2', Xianchang Yue, 23 Sep 2018
EC1: 'Comment', Robert Hibbins, 28 Sep 2018
- AC3: 'Response to the comment', Xianchang Yue, 10 Oct 2018
  - AC4: 'Response to the comment_attached files', Xianchang Yue, 10 Oct 2018

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

AR by Xianchang Yue on behalf of the Authors (19 Oct 2018) Manuscript

ED: Referee Nomination & Report Request started (19 Oct 2018) by Robert Hibbins

RR by Anonymous Referee #1 (31 Oct 2018)

RR by Anonymous Referee #2 (01 Nov 2018)

Suggestions for revision or reasons for rejection

The submitted paper is a revised version with substantial changes to the original paper. Most of the reviewer comments have been acknowledged. A Supplement is provided, with additional figures illustrating the evaluation method. Especially the discussion of the results is more elaborated, now. Nevertheless, there are still some points to clarify and I recommend the paper for revision. For example, some of the key arguments related to the connection of inversion layers and potential wave energy (new Fig. 6) need to be revised or further elaborated. Specific comments are given below.

Specific comments:
General: There are still some sentences with odd phrasing. Partly the content of the sentences is hard to comprehend because of odd word order or repetitions. Examples are p1l27-29, p2l5-7, p8l3-5, p10l19/20.
P2l17-20: Which part of this statement is only relevant for high latitudes and which for tropical latitudes? In order to keep the paper concise, you may limit the topic to tropical latitudes.
P2l21-23: If I understand correctly, you mix altitudes and seasons. This makes the sentence hard to comprehend. Please rephrase.
P4l26-28: I do not understand how the large uncertainty at the edges justifies the limitation to 30 K RMS uncertainty. The uncertainty limits should be justified by geophysics, e.g. by the amplitude of the waves that shall be resolved. In this case, the GWs often have amplitudes smaller than 30 K, i.e. the data set should generally be limited to, e.g., 10 K RMSE like described later. Otherwise nights with higher uncertainty may compromise your analysis and, e.g., produce artificially high temperature fluctuations.
P5l3/4: I understand that this method eliminates part of tidal temperature fluctuations. Please discuss the influence of remaining tidal variations with vertical wavelengths smaller than 50 km (and, e.g., 8 or 12 h period).
P5l8-10: I do not understand how the temperature fluctuation composites are made without averaging the fluctuations, i.e. reducing the wave amplitude. Please explain.
P5l10/11: From my understanding part of these inversions may in fact be remnants of GW. Meriwether and Gerrard (2004) provide a definition for MIL in terms of amplitude and persistence that should be used here, too. At least it should be discussed why it is not used and how GW and TIL are separated.
P5l12/13: Do I understand correctly that you first produce a time series of 7*24=168 h and then smooth this series by a 3h Hamming window? Is Jan 1 always day 1 of week 1?
P6l1: N^2 is indeed highly variable with season and altitude. Unfortunately I did not find a discussion of the influence of this procedure on the results, i.e. the relation of the seasonal variations of temperature, N^2 and pot. energy.
P6l7-9: From Fig. 3a I read TIL at 95 km, 90 km, and 93 km, i.e. always 1 km lower than stated here. Additionally, some of the inversions are rather weak, i.e. potentially not robust with respect to the retrieval method and not compatible with Meriwether and Gerrard (2004).
P6l9/10: Is there a objective reason why this is the mesopause but cannot be a TIL?
P7l8-10: As already written in the first review, this is not a result, but a self-evident effect.
P7l15-18: I do not understand the reason for allowing negative amplitudes. Negative amplitude has no real physical meaning. Anyway, I do not see an advantage of plotting the phases “in order”. There are indeed several phase turning points as expected from the “patchy” Fig. 4a. These patches of large N^2 agree with the TIL as expected (see above). But why do you expect the TIL (large N^2 regions) to have an AO/SAO and a specific altitude structure and how does Fig. 4d help to identify this. I am sorry, but in my eyes the phases of N^2 SAO/AO are fluctuating more or less randomly with altitude.
P8l1: The large RMSE of the phase for small amplitudes is not “odd”, but exactly expected.
P8l25: How much of this increase is due to the fact that the uncertainty of the temperature measurement increases?
P9l2: In most of the months the mesopause is well above 100 km, but the increase of energy happens already >5 km below. Therefore the Offermann et al. mechanism cannot be used to explain the increase. Furthermore, Offermann et al. (2006) describe an exponential increase of wave amplitude, i.e. linear propagation. Here, the wave is gaining energy from some (non-linear) process that still needs to be identified.
P9l14: I do not see a weaker damping of GW in winter below 94 km. But the tidal amplitude in Smith (2012) is reduced already above 80 km. From my understanding of the figures, the relation with the DW1 does not seem to be significant. Please provide further explanation or evidence.
P9l21: (The sentence misses a predicate.) The gradient of the black curve starts to change at 97/98 km, not 96 km (or 95 km where the TIL is in fact). How relates the strong gradient change of the red curve at 97 km to the arguments presented here, if there is no TIL?
P9l27-32: I think there is a general flaw in the arguments. You relate the increase of potential energy in winter-spring-summer to the strong decrease of temperature with altitude. But for autumn you find the temperature increasing with altitude above 97 km, again resulting in an increase of potential energy. In fact, the increase cannot be explained solely by the temperature profile. As shown in equation 1 there are also contributions by N and T’. In linear theory (i.e. keeping energy constant), the variation of the amplitude of the fluctuations is a result of changes of N and mean-T, but a change of mean-T may not be able to increase the potential energy. From my point of view, an increase of potential energy (if real) can only be produced by a decrease in kinetic energy or by an additional “wave source” at this particular altitude. The latter in indirectly suggested later (p11l17) by the observational filter and Doppler shifts, but this argument needs to be further elaborated and proven.
P11l10/11: I do not understand how the zero-wind line at 96 km is responsible for the constant potential energy at this altitude. Waves typically propagate from below and therefore the energy at a specific altitude depends also on the conditions below, including the wave source.
P11l15-17: While Wright et al. (2016) had wind observations available, it remains speculative whether their arguments are valid her, too.
P11l24/25: What do you mean by “decrease rate is smaller than the lapse rate”? That there is a slower decrease (or even increase) of temperatures with altitude? Or that the temperature is decreasing similar to or even faster than the lapse rate, as many people find above MILs? Please rephrase to make this clearer.
Fig sup-1: The weekly averaged data look different to Fig. 2. Data gaps are at different times of the year. The strong gradient with altitude appearing at the time of the March-tickmark in Fig. 2 comes later in Fig. sup-1. Please check and explain, if real. Furthermore, I do not understand, why the lower part of the figure is processed differently to Fig. 2. You state that “The bottom panel is the harmonic fitted result 𝑇(𝑧, 𝑡) (estimated by using (3) in the revised manuscript).” If there is some further processing using the smoothed residuals, I wonder why.
Fig. sup-2 and sup-3: The fitted seasonal variations hardly reproduce the variability of the weekly means. In other words, SAO and AO are not the dominating features of these quantities, and the true dominating features may obscure the true SAO/AO.
Fig sup-5: I strongly recommend to show this figure (together with a plot of the statistical uncertainty) in the main paper. It is necessary to understand the relevance of this study. E.g., it is very important to know that, in contrast to mid- and high latitudes, the perturbations (gravity waves) are dominated by small-scale variability and to a smaller extend by coherent wave structures (Fig. sup-5 d).

Minor/technical comments:
P4l9-11: Please make clear that these numbers are summed up over all years
P5l20: “n-month oscillation”??
P6l32: “Equation (3)”
P9l18: “more rapid”
P10l15: delete “factor of”
Fig 3c: Please plot a dotted line for the SAO in the legend.
I did not mention various typos that should be easily identifiable with text processing software.

Hide

ED: Reconsider after major revisions (02 Nov 2018) by Robert Hibbins

AR by Xianchang Yue on behalf of the Authors (14 Dec 2018) Author's response Manuscript

ED: Referee Nomination & Report Request started (21 Dec 2018) by Robert Hibbins

RR by Anonymous Referee #2 (08 Jan 2019)

Suggestions for revision or reasons for rejection

The authors again improved the manuscript in this re-revised version, following the reviewer‘s comments. Most of the topics raised in the previous review have been properly answered. Some minor topics remain. I suggest acceptance of the paper after acknowledgment of these minor comments.

Equation 3: “365/” should read “365/7.
P7l8: I think the deviations in autumn are not “minor”. Depending on the evaluation method, some inversions either vanish or change in altitude by several kilometers. Considering the more or less zero temperature gradient, I suggest to ignore the whole period between September and December. (Maybe I missed the point, but why is the temperature maximum at 97 km not marked?)
P8l2-3: Please quantify “a bit”.
P8l5: I recommend rephrasing. For example “The second reason is that the harmonic fit model is applied to weekly averages here, while it was applied to monthly averages in Friedman and Chu (2007).”
P10l16: “quantity” should read “quantitative”.
P10l30 to end of paragraph: The authors suggest that the TILs are the main driver for the GWEP increase, but this argument fails for autumn (red line), which is still not properly acknowledged. I agree that the horizontal wind might be responsible for this GWEP increase in autumn, but I think it is also responsible for the TIL. In other words, the TIL might not be the cause for the GWEP increase, but the wind. Otherwise, the autumn profiles might be hard to explain. Another topic here: I am still missing some suggestion, why the GWEP increases instead of being constant with altitude as expected for freely propagating linear waves.
P13l6: I suggest writing “September to December” instead of “October to November”, as explained above.
P13l8: I assume that this is at least partly caused by the averaging. For each single night, the gradient might be closer to the lapse rate.
Supplement: The supplementary figures now partly repeat the main figures. Please reduce the Supplement accordingly.

Hide

ED: Publish subject to minor revisions (review by editor) (08 Jan 2019) by Robert Hibbins

AR by Xianchang Yue on behalf of the Authors (15 Jan 2019) Author's response Manuscript

ED: Publish subject to technical corrections (29 Jan 2019) by Robert Hibbins

AR by Xianchang Yue on behalf of the Authors (30 Jan 2019) Author's response Manuscript

Short summary

Using 11 years of lidar temperature data, the seasonal variations (SVs) of gravity waves (GWs) are addressed in the tropical mesopause region, shown to be clearly associated with the SVs of zonal winds reported in the literature. The SVs of GWs are determined by the filtering effect of the local background wind. The altitudes of GW potential energy have a close relation to the upper mesospheric temperature inversion layers (TILs), which provides support for the formation mechanism of TILs.