The manuscript focuses on the lowermost stratosphere (LMS) based on ERA5 reanalysis data.  In the first part of the paper, trends in pressure and potential temperature of the tropopause based on different definitions (lapse rate, 2 PVU, cold point) and changes in lower stratosphere potential temperature structure are analyzed. I appreciate the authors' focus on the non-linearities in the trend due to the break in the ozone trend around 2000 using the modern DLM regression framework. However, I'm afraid I have to disagree with the authors' decision to focus only on trends in pressure, omitting trends in geometric height as I discuss in the comment below.

The second part of the paper is dedicated to LMS mass, its climatology and trends. As a novelty compared to previous studies, the authors introduce a new definition of the upper boundary of the LMS reflecting long-term structural changes. I consider this result important and valuable for further research of the LMS.

Overall, the paper is well-structured and the presentation of the results is of a high standard. However, there are two major comments from my side based on which, in my opinion, the paper needs major revision before acceptance.

Major comments:

• I find the authors' decision to focus only on ERA5 without including other reanalyses in any way unfortunate. Although modern reanalyses are improving at a substantial rate, the differences between them, especially in the stratosphere, are well known. For example, for BDC, which the authors themselves mention as a very important factor for trends in LMS, a substantial spread in climatology and trends between reanalyses was found (e.g., Abalos et al. 2015 or Šácha et al., 2024). The inclusion of other reanalyses could make the conclusions substantially stronger in the case of agreement between reanalyses, or reveal discrepancies between them. In this case, where only one reanalysis is used, I recommend a substantial expansion of the discussion regarding the known differences between the most commonly used reanalyses.
• Vertical shifts of tropopause and potential temperature levels in the paper are evaluated in the pressure coordinate system and the authors report trends in the pressures of these levels. However, the authors compare the detected trends for tropopause with previous studies from Xian and Homeyer (2019), Wilcox et al. (2012a) and Meng et al. (2021) in which trends are evaluated in a geometric vertical coordinate. Also in other parts of the paper (e.g., L215-216), the trends in pressure and altitude are interpreted as equivalent, which I do not consider to be correct as pressure levels in the troposphere shift upwards as a direct thermodynamic consequence of tropospheric warming (see, e.g., Fig. 1 from Eichinger and Šácha, 2020). So I'm concerned that comparing trends in geometric and pressure levels can be quite misleading. For example, if the pressure levels and the tropopause are moving upwards at the same rate, the tropopause pressure would not change, but the geometric height would. I would suggest redoing Figs. 2 and 4 in geometric coordinate, or the authors should show that trends in pressure level shifts are negligible compared to trends in tropopause/isentropic level height.

Minor comments:

L37: UTLS is not defined

L94-95: papers Oberländer-Hayn et al., 2016 or Šácha et al, 2024 showed that tropical upwelling does not intensify at the tropopause, but at pressure levels

L109: Do you use ERA5.1 for the 2000-2006?

L116: I suggest to change subsection 2.2 name to Tropopause detection

L117: cite ERA5 data

L117-215:  The description of detection lapse rate tropopause is, in my opinion, insufficient. Although the authors refer to the meteorology used in Birner, 2010, the clarity of the paper would benefit from a more detailed description of the meteorology and data used.  

L125-126:  I find this sentence very vague: The detected lapse rate tropopause agrees well with the ERAInterim lapse rate tropopause in Gettelman et al. (2010) and Wilcox et al. (2012b).  If a quantitative comparison was made, why is there no metric given? Moreover, the comparison refers to ERAInterim, a reanalysis from the same family as ERA5. Has validation been performed using other reanalyses? Maybe authors could cite previous studies on this matter: e.g., Hoffmann and Spang, 2022 or Zou et al., 2023.

L164: Has there been a strong dependence on the mentioned regressors? There is no discussion of the significance of the regressors throughout the paper.

L166: SOAD is not defined

L184: potential temperature trend should be 0.7 K/decade

L325: long-term

L337-338: the effect of density may be more complex due to changes in both temperature and pressure in the LMS region

Review of "Long-term changes in the thermodynamic structure of the lowermost stratosphere inferred from ERA5 reanalysis data" by Weyland et al.

In this manuscript, the authors report statistics on the rise of isentropic surfaces and mass transport between the tropics and extratropics from the ERA5 reanalysis. They use some ad-hoc criteria to define boundary regions, and mass transport is computed using the Transformed Eulerian Mean based on the formalism from Appenzeller et al. (1996).

Overall, the manuscript reads well and sounds reasonable, and I find it a nice work. However, a concern arises from the beginning, whether the authors have used here ERA5 or ERA5.1. It is now well known that ERA5 has a cold bias in the lowermost stratosphere; therefore, its data are not reliable for some time in the region of the atmosphere that is the focus here. To address this issue, ERA5.1 was produced. The authors may have used the corrected ERA5.1 data; however, they should make it explicit. If they have used ERA5, there is a chance that the results here are not entirely valid (as they are based upon data known to be erroneous), and they should update the study using ERA5.1. On the other hand, if they have used ERA5.1, this should be made explicit in the text.

Another issue: As some of the authors know (they have approached us in conferences to talk about it), some colleagues and I have proposed similar metrics to the ones here used for the UTLS region since years ago (joint PV and potential temperature changes), to determine the transition from tropics to the extratropical region (where the LMS mass is computed here), and regularly updated them. Although not published in a paper, they have been widely presented in SPARC workshops. Examples are:

- Añel, J. A., Gettelman, A., Castanheira, J. M., de la Torre, L. (2018) Tropical widening from isentropic and potential vorticity fields, SPARC OCTAV-UTLS Workshop. 7 - 9 November 2018, Mainz (Germany)

- Añel, J. A., Gettelman, A., Castanheira, J. M. (2015) Tropical widening from isentropic and PV fields. SPARC Regional Workshop on the Role of the Stratosphere in Climate Variability and Prediction, 12-13 January 2015, Granada (Spain) 

- Añel, J. A., Gettelman, A., Castanheira, J. M. (2009) Tropical broadening vs. tropopause rising. "The Extratropical UTLS" SPARC Workshop, 19-22 October 2009, Boulder (CO, USA)

These metrics are based on the equivalent latitude of cross-points between isentropic lines and the PV field, so they are especially relevant for the discussion between lines 70 and 81 and the paragraphs after line 270 (which are the same as we have shown in the past) and Figure 9 (which is precisely the same kind of plot we have been presenting). Essentially, the results we have presented in the conferences have always matched those based on the tropopause break associated with the jet for all the reanalysis (ERA-Interim, NCEP2, JRA-55 and MERRA) and WACCM4 (the CCMI version with 66 vertical levels and in a configuration with 133 levels). It is comparable to the crossing between the 350 K isoline or 2 PVU and the thermal tropopause used here. For the fairness and completeness of the discussion, it should be cited. The discussion in the Introduction in line 79, paragraphs 280-295, and the conclusions in line 367 are the right parts of the text to attribute the original idea and past results. Actually, I find it quite unfortunate that our works have not been cited in this submitted version. I have attached to this review one of our SPARC presentations to illustrate it.

Additionally, I have read the manuscript several times, and I find a gap (maybe biased by my own scientific interests) in all the exposition and discussion related to the changes in the structure of the UTLS: the changes in the structure of the tropopause itself. I agree with the authors that mass changes are the relevant variable and that they have a criterion to delimit the region where it is computed. Additionally, they mention the overlapping of the tropical tropopause over the extratropical as an issue. However, from the point of view of the lapse-rate definition, it is clear that the region studied here is changing, which is evident in the broader area of vertical stability, fingerprinted by an increase in the numbers of multiple tropopauses (e.g. Castanheira et al. 2009), correlated with increasing UTLS baroclinicity. I think it is relevant to mention this around lines 96 and 225 and, if possible, to add in the manuscript some discussion on how the metrics presented here could be related to the changes in the vertical stability and the widening of the tropopause region. 

https://doi.org/10.5194/acp-9-9143-2009.

Finally, using different periods (since 2000 and 1980) sometimes makes the text confusing. I do not see the point of beginning in 2000 and then extending the analysis back to the 1980s. Does it provide some fundamental new insight here? I doubt it. The authors could think about simply removing the part pre-2000.

Minor issues:

-Line 42: citing Hoerling et al. (1991) about the potential vorticity and the tropopause is right. However, the numbers given by Hoerling et al. limit the location of the tropopause to 1-3 PVU, which has been proven too restrictive. Hoinka et al. (1999) have a good discussion, showing that 3.5 PVU approaches extratropical tropopause better. I recommend adding a citation to Hoinka et al. so that those readers without a profound knowledge of the topic have a more comprehensive and updated view of the issue of using the PV criterion to "find" the tropopause.

-Line 43: when discussing the chemical tracers, I think it is fair to add the e90 by Prather et al., e.g. (2011) https://doi.org/10.1029/2010JD014939

Lines 88-94: I find this paragraph explicative and well-referenced. The authors mention that the issue of the BDC trends is an ongoing discussion. They refer to models, satellite data, and reanalysis. First, I would clarify in the text that Tegtmeier et al. (2020) refer to reanalysis. Then, I recommend citing a more up-to-date study, recently published by Sacha et al. (2024), which shows consistent results from models and uncertainties from reanalysis (https://doi.org/10.1029/2023GL105919).

- I would remove the explanation on the Bayesian basis of the DLM, the paragraph beginning in line 98. Also, the explanation of the accessibility to the DLM model code is already included in the "Code and data availability" section. Regarding this, a minor issue: GitHub is not a suitable repository to store assets from scientific research or papers; GitHub states it on its webpage and offers an integration with Zenodo to store code that needs long-term archival, as the one used in papers, providing a DOI for it. I strongly recommend copying the DLM code in Zenodo and citing it instead of the GitHub repository. Also, instead of making the LMS code available upon request (which outcome is never assured), I recommend depositing it in a permanent repository. ACP does not enforce this, but it is the usual practice in many other journals, including some of the EGU.

I think the colour scale for the DLM trend state in Fig. 3 should be improved. The discussion focuses on values lower than 7.5 hPa, and this is mostly yellow with independence of the values. It would be good if the authors could provide a colour palette that helps to perceive the differences between 0 and 7.5 hPa.

Lines 235-236: I would delete this mention of the polar vortex. Overall, the link between ozone recovery and its thermal effect and the material barrier that the polar vortex represents to latitudinal mixing is well-known and clear. However, I do not think it is actually relevant to the discussion here and only introduces some confusion.

- In the Conclusions, I would emphasise the "model" dependence of the results shown here for the LMS changes. There are some disagreements with previous works and probably with another reanalysis if it was checked.

General comments

The study investigates long-term changes in the thermodynamic structure of the lowermost stratosphere (LMS) using ERA5 reanalysis data from 1979 to 2019. The focus is on the period after 1998, coinciding with the onset of stratospheric ozone recovery. The research employs a dynamic linear regression model (DLM) to analyze non-linear trends in the tropopause and isentropic surfaces, examining their implications on the LMS mass. Nevertheless, the study lacks a more thorough discussion of the uncertainty of its results, see the following factors: choice of regressors (see comment below), choice of dataset (see comment below), choice of methodology (do Bayesian methods have a potential to reduce uncertainty?) etc. Based on the current review, I recommend minor revisions to address the issues outlined below. The manuscript presents significant findings and is generally well-written, but it still deserves improvement.

Specific comments

The figures are clear and support the narrative. However, some figures (e.g., Figures 2 and 4) could benefit from putting individual lines into separate panels. Furthermore, the shading in these figures denotes the associated standard deviation, however, the statistical significance is tested on top of it. I would rather display 95% confidence or credible intervals (Šácha et al., 2024) straight away.

Explain the selection criteria for the reanalysis and its period since ERA5 goes beyond the year 1979.

Why do you use only 2000 samples?

Since the authors use other regressors, I would appreciate discussion of their impact and whether they contribute to reduce the uncertainty of the discussed trends.

Using vector figures instead of raster ones may help to improve the quality of your publication.

I think the whole community would appreciate an adoption of Open Science approaches to allow the reproducing the extensive analysis in this study (e.g. Laken, 2016), especially when authors use DLMMC which has been made open. In particular, I would recommend any kind of willingness of the authors to publish the code allowing to reproduce the figures in the paper. There are multiple ways how to proceed, either to allow access upon request or via portals allowing to assignment Digital Object Identifier (DOI) to the research outputs, e.g. ZENODO. I think it could enhance the quality and reliability of this publication.

Technical comments

l11 0.5° latitude per decade?

l166 replace SOAD with SAOD and define

References

Laken, B. A. (2016). Can Open Science save us from a solar-driven monsoon? Journal of Space Weather and Space Climate, 6, A11. http://doi.org/10.1051/swsc/2016005020.

Šácha, P., Zajíček, R., Kuchař, A., Eichinger, R., Pišoft, P., & Rieder, H. E. (2024). Disentangling the advective Brewer-Dobson circulation change. Geophysical Research Letters, 51, e2023GL105919. https://doi.org/10.1029/2023GL105919