This paper assesses the usefulness of satellite-measured atmospheric temperature and humidity for convection prediction. The assessment is based on surrogate data as opposed to real measurements. Specifically, global reanalysis data are sampled according to the sampling pattern of a polar orbiting satellite, to mimic the retrievals of an infrared hyperspectral sensor, AIRS. One interesting aspect of this investigation is the use of a trajectory model, which was introduced in an earlier work (Kalmus 2019), to increase the spatiotemporal representativeness of the satellite measurements. The paper is logically organized and well written, providing sufficient technical information and clear descriptions of the results. I do have some concerns, as detailed below, on several aspects of the paper, including the design of the research, the method, and the interpretation of some results. I think this paper could add excellent contribution to the literature after these comments are addressed.

L30-35. Two points are provided as the motivation of this work: weather and climatology. These starting points probably need to be reflected on or revised. For the objective of improving weather forecast, since the trajectory relies on NWP-model modelled winds, how could this approach have any advantage over the data assimilation approach? For the objective of studying convection climatology, why not simply use the reanalysis data without reducing the sampling to match AIRS?

L82. An important claim is made here about AIRS being advantageous for studying climate trends compared to reanalyses. This point needs to be better discussed, as one can easily come up with counterarguments. For example, given that the conventional retrievals typically take prior information including first guesses from analysis, it is not obvious to me that the retrieval products aren't subject to the same issues as reanalyses. A general comment is that I think the paper can provide better reasoning or more references to establish suitability of AIRS for studying climate trends. For instance, do you think the radiometric stability of AIRS together with its spectral information may facilitate detecting convection regime changes, taking advantage of their spectral signatures (e.g., Huang and Ramaswamy 2008, https://doi.org/10.1029/2008GL034859; Kahn et al. 2016, https://doi.org/10.1002/2016GL070263)? Or, may methods particularly designed for climate trending, such as the average-then-retrieve approach (e.g., Huang et al. 2010, https://doi.org/10.1029/2009JD012766; Kato et al. 2014, https://doi.org/10.1175/JCLI-D-13-00566.1) be of relevance here?

L129. A critical methodological question here is whether ERA5 profiles can appropriately represent the vertical resolution of AIRS retrieval or its ability in measuring such quantities as CAPE. I'm surprised that this important consideration is completely neglected. The paper would benefit from a proper discussion of this issue or an assessment of the impacts, for instance, by using the AIRS averaging kernels. 

L155/L319. What "neglected processes" are referred to here?

L205. A relevant question of interest is how much the 1:30am/pm overpass times of AIRS limit the convection prediction. Or, what different times would be more useful? Can this study provide some insights?

L292. The poor prediction of the temperature of the upper layers (fig. 7c) is surprising. Why?

L321. Is this really surprising since diabatic heating tends to be balanced by adiabatic motion at grid (or large) scales? And, again, clarify what's "neglected". Another philosophical question here is that there is equal amount (50%) of unexplained variance – this raises many questions:

how does this limit the usefulness of the prediction, and in what situations - for example, what regions or weather systems are missed? 

L447. Following this reasoning, shouldn't the analysis and comparison be limited to times prior to convection?

My background is in trajectory calculations in the upper troposphere and lower stratosphere.

Based a method reported by Kalmus et al. (2019), this paper proposes an interesting extension to improve predictability of strong convective events from daily sun-synchronous satellite profiles by coupling with forecasts of adiabatic forward-trajectories. The paper assesses a proxy setup against ERA5 reanalysis data for the year 2019 over a part of the United States. Broader implications of the work are realised in the discussion. The results and discussion are well-written and scientifically reasonable, however I found the introduction somewhat hard to follow and some of the methods unclear. Overall, the paper is suitable for publication with ACP, however there are some specific comments that need addressing, listed below:

L64-65: Whether ERA5 is a reasonable representation of AIRS should be described. For instance, does ERA5 assimilate AIRS retrievals?

L187-188: The WRF 27km datset should be introduced appropriately. From looking around, it appears to be a series of daily forecasts and not an analysis dataset (which would prompt other questions), but the text should explain this.

L197-200: I'm a bit confused about the local enhancement metrics, mainly their names dMU_CAPE and dMU_CIN. How are they calculated for ERA5? You do not calculate the most unstable parcel for ERA5, so is dCAPE a more precise label in that case? Or are you using MU_CAPE from ERA5-FCST for the baseline in all cases? Please explain in the text somewhere, and consider the labelling convention.

L391 and Fig 12 caption: What is meant by time-matched? I guess you mean some sort of integration over all timesteps shown in Figs 10 and 11, but it isn't explained in the text. As part of this, I am not quite sure how you show ERA5-overpass in Figs 10 and 11 for each hour, surely you have only one set of ERA5-overpass tp values (are these the same as ERA5-FCST at t0?), I guess it is the histogram bins that are changing with hour. Again, this should be clarified in the text.

L465-467: Do you have references to support these two sentences?

Data and code availability: In line with the ACP data policy, the data underlying the results in this paper should be FAIR. Please provide a link to a copy of the ERA5-FCST data you generated, and if possible the analysis scripts too. Either a preliminary link for reviewers to consider, or a link to a FAIR-aligned reliable public data repository.

Specific comments that do not need addressing:

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The terms pre-convective and pro-convective are similar and risk confusing the reader, I would suggest rephrasing one or the other.

L240-243: Could the use of maximum unstable CAPE for ERA5-FCST be causing the higher values relative to ERA5 CAPE? If it was possible to calculate MU-CAPE for ERA5, would that also be higher? Or, how does MML CAPE for ERA5-FCST compare with ERA5 CAPE?

L283-284: The argument in support of ERA5-FCST would be clearer if you could show the changes to CAPE at the different levels. Does the CAPE gained around ~800hPa outweigh losses to T-q biases near the surface?

Fig 8: The points made in the text are strong ones, but there might be a more appropriate figure. If the motivation of the eventual ERA5-FCST product is to predict hazardous convective weather, then Fig 7 is more meaningful than Fig 8, where the biases are more apparent, however it is shows a single event only. Might it be more insightful (as supplementary material) to show a version of Fig 8 restricted to periods of high-CAPE or high precipitation?

Technical corrections:

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L64, L78, L94, L144, L269: Tidy citation parentheses.

L205: Should there be a word before CAPE? low/high?

L205-207. This is an important sentence but is quite hard to follow. Consider rephrasing.

L219: A word seems to be missing from this sentence.

L239: Reference order for Fig 3b and 3c needs correcting.

Fig 8 caption: Please mention the time period being calculated over.

Data and code availability: Please include SHARPpy and the WRF27km dataset.

Supplementary figs: These refer to ERA5-AIRS-FCST, is that ERA5-FCST in the main text? Please check for consistency.