Review of Juusola et al., Drivers of rapid geomagnetic variations at high latitudes, submitted to    EGUSphere, 2022

General Comments

This is a very well written study of five of the strongest geomagnetic variations observed by the IMAGE magnetometer array.  It has a very good introductory review section, followed by tables showing the largest ΔH and |dH/dt| at each of the IMAGE sites, separated into total (observed) and external and internal contributions.  This is followed by a detailed analysis of five events that produced some of the most intense external |dH/dt| values.  The authors provide plausible interpretations for the magnetospheric/ionospheric phenomena that drove these events, and also provide a careful discussion in section 4 of some of the limitations of this study (even though it is based on a large volume of data) and of continuing challenges to the successful prediction of intense (dangerous) |dH/dt| events.  It concludes that the relevant scientific community is still far from a full understanding of the detailed physical pathway(s) leading to either modest or extreme |dH/dt| events, much less to the prediction of the time and place where these events will occur.

The content of this paper is of high quality and is certainly appropriate for publication in EGUsphere.  This reviewer has only two substantive comments and four more minor comments. 

Specific Comments

It is strongly suggested that throughout the paper the magnitude of the perturbations in the horizontal magnetic field that are denoted |H| should be replaced by |ΔH|.  The magnitude of the total magnetic field or even its horizontal component (in a given coordinate system) is not what is physically important; it is rather the change in its value (during some appropriate time interval). 

Lines 375-391:  The manuscript cites a study by Viljanen et al. (2006b) that showed peaks in occurrences of large |dH/dt| events 5 minutes after both non-storm and storm-time substorm onsets at Sodankylä (63.92° MLAT) and Nurmijarvi (56.89° MLAT) during 1997 and 1999 (their Figure 3).  However, there were no substorm onsets or sudden intensifications of the western electrojet during the five selected events.  The authors may wish to contrast the observations of Viljanen et al. (2006b) with those of Engebretson et al. (2021), who showed in their Figure 2 plots of maximum dB/dt events (all > 6 nT/s) vs. time delay after substorm onsets for five stations in Arctic Canada during 2015 and 2017, with MLATs ranging from 75.2° to 64.7°.  There was no significant peak near 5 minutes after onset at any of these stations (the distributions were relatively flat during the first 30 minutes).  The distribution at each station had a gradual and extended falloff that was roughly consistent with those shown in most panels of Figure 3 of Viljanen et al. (2006b).  The Engebretson et al. (2021) study also showed in panels B and C their Figure 11 that postmidnight dB/dt events that occurred greater than 30 minutes after substorm onsets at the lowest latitude station (KJPK, 64.7° MLAT) occurred during periods of gradual increases in the SML index (weakenings of the WEJ). 

Engebretson, M. J., Ahmed, L. Y., Pilipenko, V. A., Steinmetz, E. S., Moldwin, M. B., Connors, M. G., et al. (2021). Superposed epoch analysis of nighttime magnetic perturbation events observed in Arctic Canada. Journal of Geophysical Research: Space Physics, 126, e2021JA029465. https://doi.org/10.1029/2021JA029465

Technical Corrections

In line 185, the phrase “optimal temporal development” does not seem appropriate.  “Optimal” approximates to “best,” so this part of the sentence is confusing. 

Figure 4 needs to be much larger in the final published paper, and some of the fine print in the figure could be moved to the figure caption.  Figures 5, 6, 9, 11, 13, 14, 16, and 17 would also be easier to read if they made use of the full width of the available space on a page. 

In line 285, “possible” should be changed to “possibly.”

In line 375, remove “of” after “five.”

I am sceptical of the authors' measures of internal and external geomagnetic field variation.

I am happy to be corrected on this, but I see no reason why the variational data could not, in principle, be fitted with a geomagnetic field model that are entirely generated by external current systems. When I say this, of course, I am not referring to the internal field generated in the Earth's core. That part of the field is essentially steady over the course of a magnetic storm. To emphasize, I'm referring to the storm-time variation in the geomagnetic field. I see no reason why that part of the field can't be entirely modelled by external sources.

In this context, recall that a spherical-harmonic description of a global field has both internal and external parts (the division between the two comes with different radial functions), and this dichotomy is consistent with potential-field theory. That sort of internal-external division is rigorous, but such a division is not, to my knowledge, available for spherical elementary currents , where one starts off assuming that internal currents reside on a shell at an arbitrarily chosen depth.

Therefore, I would be extremely careful in making physical interpretations of the *internal* field while relying on an unrealistic assumption about the source of the internal field. The danger of circular reasoning, here, should be clear.

I note that the authors seem to admit most this on lines 248-250: "However, separation and interpolation of the geomagnetic field between the stations are not perfect and are affected by the density of the magnetometers as well as boundary conditions, as discussed by Juusola et al. (2020)." One wonders, then, how much the separation can be affected by the boundary conditions. This big issue is not addressed anywhere as far as I know.

My understanding is that the boundary conditions used in spherical elementary current systems are just mathematical conveniences. As such, they allow construction of specific field models, but these field models are only examples from the large set of models that can fit the data. In other words, the models are non-unique. Some of the possible models (with different chosen boundary conditions) might have lots of internal contribution, but others might have very little.

This sort of non-uniqueness is why spherical elementary currents are often described as "equivalent".

As long as such non-uniqueness exists, I don't know how the authors can come to any conclusions about the relative portions of internal and external fields.

Please consider these issues.

A review of the manuscript entitled

“Drivers of rapid geomagnetic variations at high latitudes”,

submitted to the journal EGUsphere by Liisa Juusola et al.

This is a very promising research paper. It exploits the large and comprehensive data resource that is the IMAGE archive. It employs an under-utilized, if not particularly new, analysis technique with 2-layer 2DSECS. It uses these to separate “internal” from “external” equivalent current sources driving geomagnetic disturbance at Earth’s surface, and therefore to better understand the impact and scale of magnetosphere/ionosphere dynamical phenomena without worrying that “large” geomagnetic disturbances are simply due to much more localized earth conductivity structure. It is also very interesting to see how “internal” sources contribute to the interpretation of space weather phenomena, although perhaps this topic was covered in more detail by a recent paper by the same 1^st author, and is only a secondary consideration in the present manuscript. Altogether, this manuscript offers a novel perspective on what influences ground magnetic disturbance the most, for the most impactful space weather events, and therefore should be published and added to the scientific literature base through EGUsphere.

That said, the presentation of this material lacks a certain focus, and is, at times, difficult to read, even for a scientist who is well-acquainted with the analysis techniques and scientific subject matter. The comments below are offered in the constructive hope that the overall clarity and readability of this research paper will be improved, and ultimately appeal to a wider and possibly more scientifically diverse audience.

These critiques/recommendations are offered in a loosely prioritized order:

1. There is a considerable review of the underpinning theory in the Introduction. It ends with an overly brief statement of the question being asked/answered, and it is not especially clear how this relates to the material presented prior to that.
   • most of the theory could be migrated into a more fleshed out Section 2.2, including Figures 1 and 2;
   • the introduction could then more clearly and succinctly articulate the motivation behind this study, possibly hinting at the more comprehensive explanation of techniques coming up later.
2. There are too many figures (18!), and many figures include multiple labeled panels, sometimes up to the letter “l” (i.e., 12 panels!). This alone is very distracting, but the real problem is that it is not obvious that all the panels are discussed in the body of the manuscript. The authors should reconsider whether all these are necessary, and if so, could some be migrated to supplementary material. If the authors choose to keep most or all figures, they should make almost all of them larger, probably full-page.
3. There are too many inline mathematical relationships. The authors should consider changing some of these to numbered equations that are visually separated from the main text, then cross-referenced when needed.
4. Similarly, there are too many statistics and other data presented inline that would be more clearly presented in numbered, tables, then cross-referenced when needed.
   
   
   
   (some specific comments and questions that should be addressed)
   
   
   
   
5. Authors should expand on, or cite specific literature that justifies, the statement in the Introduction: “The down component (Bz) cannot be included in the fitting, because it cannot be represented in terms of ionospheric equivalent currents only”.
6. Authors should explain, or cite relevant literature justifying, why the internal 2DSECS was defined at only 1m depth? This certainly deviates from much of the previous literature (e.g., Pulkkinen et al., 2003 – EPS), and it seems likely to bias results toward nearby geomagnetic measurements.
7. The authors should explain better how the results presented in Figures 7 and 8, and related discussion about the data’s time resolution, tie into discussion of internal and external sources, and localization of |dH/dt|. Frankly, while this is an important point, it seems like a topic for a different paper.
8. All references to the supplemental animations/movies should make it clear that these are supplemental material. If they could by hyperlinked, even better, at least for the online version of this manuscript.
   
   
   
   (typos, grammatical errors, and ambiguities I noticed)
   
   
   
   
9. Line 43 – “in order to be able to produce--d-- the highly structured…”
10. Line 73 – “…by solar wind perturbations, or internally.” Clarify “internally”.
11. Linen 87 – “…rapid dB/dt spikes…” – maybe quote dB/dt, assuming it is taken from the cited paper, since the authors consistently use |dH/dt| in this manuscript.
12. Line 375 – “What is noteworthy in our five --of-- events is…”