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March 14, 1997

Dr. Robert B. Sheldon
Center for Space Physics
Boston University
725 Commonwealth Ave
Boston, MA 02215

Re: "A new magnetic storm model" (GRL ms. #6841 revision)

Dear Dr. Sheldon,

Enclosed are three reviews of your revised paper. Two are by Referees A and B, who also evalueated the earlier version of the paper. The third review is by a new referee (C), to whom I made available, in addition to the revised paper, the comments of Referees A and B on the first version of the paper and your responses.

As you can see, Referees A and B are not persuaded by your responses to their earlier criticisms and remain skeptical of the model that you propose. Referee C raises a number of apparently substantive questions but finds "that the model has merit and that it appears that it could well be a reasonable explanation of the observations." However, he also feels that a convincing case for your model requires a far more detailed discussion of both the data and the model than can be accommodated in a GRL article. On this point all three referees are in complete agreement.

Despite their skepticism about your model, Referees A and B both acknowledge that the observations you present in your paper are significant and interesting. Both suggest that a report of these data alone would constitute a good GRL paper. (Referee C made the same suggestion in the covering letter to me that accompanied his/her report.)

It is clear from the reactions of all three referees to the paper that the presentation of your model belongs not in GRL, but in JGR, where it can be developed in the detail required to convice--perhaps--those members of the community who, like Referees A and B, will react initially with skepticism. For this reason, I am afraid I must decline the present version of your paper. I urge you to consider carefully the comments and criticisms of all three referees and address them in an expanded, more detailed paper for submission to JGR.

At the same time, it is clear that the data you present and the event they describe are interesting and unique. I would therefore encourage you to submit for our consideration a paper that simply presents these data without trying to make a case for a controversial model. Although the focus of such a paper would be on the data, it would, as Referee A points out, be appropriate to conclude the paper with some speculative comments about the interpretation of the data.

Thank you for considering GRL. I am sorry that the outcome of the reviewing process ws not the one that you and your co-author had hoped for.

J.H. Waite, Jr.

Referee A

Referee's Remarks on "A New Magnetic Storm Model", by R. B. Sheldon and H. R. Spence

General Comment

I have carefully read over the author's responses to my previous review and find that the paper still makes a number of claims, central to the proposed storm model, without sufficient observational or theoretical support. I find this criticism to be quite explicit and not "implied" as the author suggests in his reply. Details to substantiate this criticism will be given below in evaluating the author's responses.

The presentation of the magnetic storm model as a viable mechanism seems to be a bit premature requiring significantly more theoretical development and observational support for its component parts. I strongly urge the author to present the GRL paper as a report of the observations, which are quite interesting, and include a paragraph at the end in the discussion section speculating on their interpretation, to be followed by a more complete treatment of the model, proposed here, in a JGR article. Having made this recommendation, I will nonetheless return to the present paper and respond to the author's comments on my previous review.

Responses to the author:

(1) The author's response is sufficient ot convince me that a storm may have occurred at this time though it was a very short-lived event and highly asymetric. The fact that the "provisional" Dst disturbance was atypical in that it lasted only about 1 day ans was extremely asymmetric may be an important piece of information in understanding and interpreting the observations, though it is up to the author whether or not he chooses to include some discussion of this.

(2) The signature in the IPS energy time spectrogram (on the CEPPAD web site) appears to be a nose event as the author suggests. However, turning to observations for the moment, the nose event (peaking at 30 keV) in the Kozyra et al. [1993] paper occurred during a storm with minimum Dst ~-60nT, maximum Kp = 6+, and the estimated peak cross-polar cap potential difference was 161 kV. the April 15 event had very similar minimum Dst (-63 nT?), maximum Kp (7) and estimated cross-polar cap potential difference (>150 kV) values though it was much shorter in duration. Why should the peak energy of the nose event ions be ~90 keV? It cannot be simply a matter of cranking up the electric field if the storm conditions are similar. This is an interesting piece of the puzzle. Modeling of the ion trajectories to establish that this is definitely a nose event would make a much more convincing case. But if this is not possible for this initial report, at least some discussion of the characteristics of this event compared to other nose events in the literature would be helpful.

As a side point, Wodnicka [Planet. Space Sci. 37, 525, 1989] claims to have reproduced Ejiri's [JGR, 83, 4798, 1978] trajectories.

(3) The composition of the 30 keV population is important, in the sense that you would like to explain the temporal history of the O+ component of the ring current with this unifying storm model. After thinking over the authors remarks, I can accept the arguments that the author presents for assuming the 30 keV ions have a major O+ component. However, the 100 keV ions also have a significant O+ component which implies the plasma sheet source population was enriched in O+ prior to the nose event. What are the relative strengths of the two sources of O+ and how does this fit into the proposed storm model?

Regarding the O+ charge exchange lifetimes, the lifetime for equatorially-mirroring 100 keV O+ at L=5 should only be about 2 days, at L=3-4 less than 1 day. The CAMMICE measurements were made 3-4 days later. At what L value were these measurements made?

Lastly, CEPPAD was not designed to detect O+ ions. If the lower energy ions are indeed oxygen, it is my understanding that there is an energy threshold below which these ions cannot penetrate into the CEPPAD instrument. What is this energy threshold and could this produce a seemingly monoenergetic distribution because ions below this threshold though present were unable to access the detector.

(4) The author is not simply reporting on the observations and speculating that a field-aligned potential could produce this signature, he is asserting that the potential exists and using it as the basis for a storm model which explains a host of subauroral signatures. The existence of a 30 keV field-aligned potential at such low L values is essential for the claims that the author makes throughout the paper to be valid. The author claims that such a solution exists (though counterintuitive) under certain very restrictive conditions but can offer no observational proof that these conditions have occurred. At the very least, semi-empirical models of the thermal plasma density might be used to establish that the required conditions are possible on the field lines in question.

The main focus of the paper is on the storm model and at this point it is a "house of cards". the assertions of the paper go too far without a better theoretical and observational foundation for the existence of a field-aligned potential of this magnitude on plasmaspheric field lines, and for the proposed association with SAIDs, accelerated electron distributions in the subauroral region and upflowing subauroral oxygen beams.

(5) After reading the authors remarks, I looked back at sevveral SAID papers and found that they indeed have been observationally linked to substorms. The reason that I assumed that they were linked to storms is that the current theory explains them on the basis of the closure of region 2 currents through conductivity gradients at the edge of the diffuse aurora in the ionosphere [Anderson et al. JGR, 96, 5785, 1991; Anderson et al., JGR, 98, 6069, 1993]. A component of region 2 currents has been associated with the partial ring current.

The link between nose events, 30 keV field-aligned potentials and SAIDs is an unsubstantiated portion of this paper. The signature of accelerated electrons (< 32 keV), that would indicate the existence of a potential drop on SAID field lines, has been looked for on several occasions, and not found, using DMSP and DE-2 observations. This was presented in Phil Anderson's thesis. However, it is certainly worth looking for signatures in the ionosphere associated with the April 15 event and others like it. Riometer signatures to my knowledge have also not been associated with SAIDs. Please give a reference for this association before using it as evidence for the presence of SAIDs. There are characteristic zones of ion precipitation (many 10's of keV to MeV) that move to low L values and intensify during storms. These zones have not been associated with SAIDs but appear to result from violation of the first adiabatic invariant on stretched magnetic field lines [c.f., Sergeev et al., JGR, 98, 7609, 1993]. These would certainly produce a signature in the riometer even if no SAID was present. For the April 15 event, the presence or absence of SAID signatures should be established and the details of the precipitating electron distribution established using readily available DMSP and NOAA observations which extend to 30 keV before parallel potential drops are proposed as their cause. Also it would be very interesting to know the location of the discrete auroral oval in relation to the accelerated ion beams that apparently exist in the data.

(6) (a) I disagree that the temporal correlation between Dst and the O+ content cannot be explained by sources of O+ other than the 30 keV parallel potential drops discussed here. As the convection picks up, Cladis showed that the cleft ion fountain deposits oxygen ions over a smaller L value range and closer to the Earth than during times of slower convection. This results in a very pronounced Earthward gradient in the O+ content which is then convected inward to form the ring current with an associated temporal history. Timing problems associated with the rapid appearance of O+ in the inner plasmasheet prior to storm main phase are alleviated somewhat by the fact that Kp is usually elevated to some low level for a time prior to storm main phase. In the case of the April 15 event, Kp was 3-4 for some time prior to the rise of Kp to 7 in the interval 21-24 UT on April 14. In addition, oxygen ion beams moving up auroral field lines rapidly bring oxygen directly into the near-Earth plasma sheet. This is the mechanism that Iannis Daglis proposes for the fast time-scale increase in the oxygen component of the inner plasma sheet (7-9 Re) seen in AMPTE/CCE observations [Daglis et al., JGR, 99, 5691, 1994].

(6) (b) I was not suggesting that the author perform such a statistical study but that he might get an idea of the morphology of upflowing O+ with L value by looking at past work in the literature. Andy Yau working with Bill Peterson and Ed Shelley did several statistical surveys of upflowing O+ beams using the DE-1 EICS instrument which measured ions over the energy range 0.1 - 17 keV/e. Granted this is at slightly lower energies than the beams presented here. As I recall, the occurrence frequency of upflowing O+ at low L values was small. Variations with magnetic activity were also examined. If direct injection of upflowing O+ beams are a major source of ring current ions, one should find evidence for such a source in these statistical studies. After all nose events with peak energies of 30 keV definitely occur and would produce field-aligned potentials with values within the DE-1 EICS energy range.

(7) It is not necessary to debate the details of theories and observatioins of ion cyclotron waves in the dusk sector for the purposes of this paper, and I apologize to the author for beginning such a discussion in my previous comments. If, as you say, ion cyclotron waves are produced by these upflowing ion beams, then there should be clear evidence for this in the POLAR wave measurements. Such observations would lend important support to the storm scenario the author proposes.

Referee B

Referee (#B) report on the revised GRL ms. #6841: "A new magnetic storm model," by Sheldon and Spence

To repeat from my first review: the data presented in the paper are significant, and a presentation and general discussion of these data, including even speculations on field-aligned electric fields, is certainly suitable for a special GRL issue on ISTP. Unfortunately, my principal original objections to the present paper still stand, and thus I cannot recommend the paper in it[s] present form.

In the first paragraph of their response to my original comments, the authors indicate that they have somehow convinced themselves that for a trapped or isotropic pitch angle distribution (assuming initially no field aligne[d] electric fields) the density will peak off the magnetic equator. It is a straightforward exercise to demonstrate otherwise. What the authors are saying is that if one begins with a quasi-neutral plasma, and then injects positively charged ions with a density distribution that strongly peaks at the magnetic equator, the system will respond with an electric field that tries to force even more ions towards the equator. I am open-minded enough, I think, to believe that occasionally 2 + 2 = 5 in science. However, the person making the claim of such an astounding conclusion must accept the burden of proof. These authors have refused that burden. They have in effect stated: "go prove it yourself." The fact that it may not be practical for the authors to accept this burden within the confines of a short GRL letter is all the more reason that this paper is not appropriate for GRL in its present form. I would suggest that the authors expand their presentation to whatever length it takes to prove their point and then submit it to JGR. I stated in my original review what kind of presentation it would take for me [to] recommend acceptance of the authors' paper.

Referee C

Comments on GRL MS 6841: A New Magnetic Storm Model, by Sheldon and Spence

The magnetic storm model that the authors propose in this paper I find to be interesting and attractive. It puts together a chain of processes that are triggered by a large cross-tail electric field caused by a large increase in the solar wind pressure together with southward turning of the IMF Bz for some significant period of time. They propose that magnetospheric ions are convected toward the earth from the tail with a selected group at the appropriate energy penetrating deeply into the inner magnetosphere. These ions then generate a parallel electric field in a narrow L-shell band (because of the excess psitive charge) which accelerates electrons to and extracts ionospheric oxygen from the ionosphere. They are led to this model for a storm by their data which shows a penetrating band of ions near 90 keV ("nose protons") and a band of field-aligned ions near 40 keV which appear to be correlated in energy and intensity with the 90 keV band.

The model is attractive because it invokes a set of known physical processes and ties them together sequentially so that there is a causally linked chain of events that can be investigated theoretically and compared with observations.

I believe that the model has merit and that it appears that it could well be a reasonable explanation of the observations. However, both the data and the model require detailed treatment in order to make a convincing case, and I do not think that it is possible to do justice to the model and to the comparison with the observations in a four-page GRL paper. It appears that this is also the main reason why the previous reviewers had problems in recommending the paper.

Thus my recommendation is that the authors do a detailed treatment of the basic processes which are involved in the model, using their data as the basis for the treatment, and put together the kind of substantial paper that would be appropriate for a possible major advance in the field, and submit it to JGR.

I will list below some of my comments and questions regarding each of the basic processes they invoke:

(1) On the large induced cross-tail electric field

What is the threshold on the enhanced IMF Bz magnitude, direction, and duration in order for saturation of the tail's ability to shield the polar cap potential to occur? Is this well known (then it should be documented) or can this be demonstrated?

(2) On the ion nose events:

It is difficult from the spectrograms to get a good idea of the actual energy and pitch angle distributions, for both the 90 keV and the 40 keV bands. (This is a problem with a short paper--not enough room to do justice to the data.) How near 90 degrees do the beam ions have to be in order to form a nose event? The authors also need to document their statement that nose events are highly correlated with storms.

(3) On the 40 keV beam ions:

The monoenergetic 40 keV ions are really not very monoenergetic since their FWHM is about 35 keV. What is the pitch angle distribution of these ions--is this also quite broad? Nevertheless the constant ratio of (nose/beam) energies is supportive of the idea that the beam is related to the nose ions. But what about the time scales involved, since this is a very dynamic event? If the beam ions come from the ionosphere, one would think that the ratio would decrease over time as more ions are pulled up from below, unless this all happened quite quickly at the beginning of the storm. What stabilizes the ratio? This needs to be addressed.

(4) On the parallel electric field:

The authors appear to be mixed up between the potential gradient and the electric field. If the nose ions generate an excess of positive charge away from the equator, then there will be a positive potential at a point away from the equator which means that the potential gradient is positive away from the equator but the electric field is negative (pointing towards the equator). This has the required effect of pulling electrons away from the equator and pulling ions out of the ionosphere if indeed the electric field extends far enough along the magnetic field line to reach the oxygen ion populations. This is an important question since the authors are proposing that the parallel electric field may involve a double layer. If the double layer is located well above the ionosphere with little electric field below, then it is hard to see how a significant ion population can be extracted.

The question of how the parallel electric field is generated needs to be addressed in some detail. The pitch angle distributions of the nose ions and of the beam ions is of particular importance, since the ion density dominates the generation of the electric field according to the mechanism which they invoke, and the density of mirroring particles along a field-line is determined by the pitch-angle dependence. It seems unlikely that there could be a significant contribution to the ion density from such a high energy (i.e. 90 keV) ion population. Thus it seems doubtful that any parallel potential drop would be at a significant fraction of the full nose ion energy.

The statements at the end of the 2nd paragraph on page 5 (complete expelling of electrons from equator and then neutralization at some point where a double layer occurs) need to be put on a firm basis. The introduction of a "Chapman Layer" is puzzling since this is the only equation in the paper, but the terms are not defined nor is the expression used for anything. If the extraction potential is extended over distance, as stated, this would seem to contradict the idea of a double layer. Also, the process of "shielding" by neighboring flux tubes is again something that needs to be either worked out or juustified somehow if it is important to the chain of events.

(5) On the riometer absorption:

The relation of the observed riometer absorption (page 6) in a "narrow strip in latitude" to the latitude of the parallel electric field should account for the fact that both the nose ions and the beam ions are seen over a reasonably large range of L-values (L = 5.2 to 3.3), which translates into a magnetic latitude range on the earth from about 63 to 57 degrees. Does this latitude range agree with the riometer data? It would be helpful to see what the riometer data looks like.