GEOPHYSICAL RESEARCH LETTERS

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November 22, 1996


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)

Dear Dr. Sheldon,

Enclosed are the reviewers comments on your paper. As you can see, the reviewers have concerns about the validity of this work. Therefore, I must conclude that this paper is not converging toward publication and that further handling of it in its present form is not warranted. As significant additional work appears to be required to render the paper acceptable, we would treat any revised version of it that you may wish to submit as a new submission, with a new received date and manuscript number.

I am sorry that the outcome of the reviewing process was not the one you had hoped for. Thank you for considering GRL.

Sincerely,
C. Farmer
for J.H. Waite, Jr.

Referee A

Comments on "A New Magnetic Storm Model", by R. B. Sheldon and H. R. Spence

General Comments

The authors present a scenario for magnetic storm development on the basis of observed monoenergetic ion signatures in the CEPPAD instrument. The central element in this model is the production of field-aligned potential drops in association with nose events in the ring current. These potential drops then accelerate heavy ions out of the ionosphere to populate the ring current and produce a whole suite of subauroral signatures. Though this is an interesting model, the authors offer very little evidence that any of these processes are actually occurring and the evidence that is presented is largely weak and circumstantial. In addition, the Dst did not vary in the typical manner that one would associate with a magnetic storm during the time interval of the CEPPAD observations but is more consistent with plasma injection penetrating in only to relatively high L values, never becoming part of the ring current, but drifting to the magnetopause boundary and being lost. (The Dst, which was not shown in the paper, decreased to -48 nT over a period of a few hours then recovered rapidly within a few hours. The asymmetric component of the Dst decreased to nearly -200 nT during this same interval and rapidly recovered.) How does one construct a magnetic storm model on the basis of data taken during this very weak perturbation in Dst which does not really appear to be a magnetic storm? Without more concrete substantiation of the various claims made in this paper, including some verification that a magnetic storm actually occurred during this interval, I cannot recommend publication.

Specific Comments

Page 3, paragraph 3
The authors identify the 90 keV ion peak as a nose event on the basis of its trapped pitch angle distribution and monoenergetic nature. However, a study of the penetration of newly injected ring current particles by Ejiri et al., (JGR, 85, 652, 1980) demonstrated that 10-30 keV ions penetrated the deepest into the magnetosphere. The sharpness of the energy peak in the ions was a function of local time being very broad in the 24 MLT sector and much narrower in the dusk sector. A nose event observed by AMPTE/CCE during a storm in late September 1984 showed a very pronounced peak at 30 keV in agreement with these results (Kozyra et al., 1993). The nose event identified in this paper was in the 0 MLT sector and thus should have been difficult to pick out because of its broad spread in energy. In addition, the authors must demonstrate that the deepest penetration should have occurred for 90 keV ions (as opposed to much lower energies) under the existing magnetospheric conditions.

Page 4, paragraph 3
This is very weak circumstantial evidence for O+ beams during the CEPPAD observations [sic] period.

Page 4 paragraph 4
As I recall from the published literature on nose events, they always penetrate into the plasmasphere. What exactly is the thermal electron density? It seems to me that at L values near 4 on the nightside during very weak magnetic activity, the electron densities could be substantial. This is a critical point, since you require very low cold electron densities or the field-aligned potential will be rapidly shorted out.

Why do you require monoenergetic ions to produce the field-aligned potentials? Ring current ions in general have very trapped distributions and therefore the mechanism you propose should generate field aligned potentials everywhere in the ring current region where thermal electron densities are low and the ring current electrons have a substantially different pitch angle distribution than the ring current ions.

Page 5. Paragraph 3.
I believe that SAIDs have always been associated in the literature with storms and in fact most generation mechanisms center around processes associated with ring current shielding of the inner magnetosphere. The signatures associated with SAID events were well documented by the Dynamics Explorer spacecraft. In the observational literature regarding SAIDs, that resulted, is there any evidence for signatures associated with field aligned potentials? I do not recall any reports of O+ ion beams occurring on SAID field lines but only upwelling O+ ions associated with low altitude heating by the SAID electric fields. Is there evidence of a SAID event coincident with the monoenergetic ion peaks in the CEPPAD data? If not, why is this relevant?

Page 6, paragraph 2
The dependence of the O+ content on Dst can easily be explained by the observed substantial O+ outflows from the cleft ion fountain. Why are subauroral O+ beams required to explain this dependence on the directly driven component of magnetic activity? How frequently were subauroral O+ beams observed by Dynamics Explorer and how substantial were the O+ fluxes associated with those beams? My recollection is that they were only occasionally observed but were not a major component of the total O+ outflows. Since a large body of observations exist on O+ outflows, it should be easy to verify observationally the magnitude and frequency of O+ beams at subauroral latitudes. However, verifying their association with ring current nose events is another issue entirely.

Page 6. paragraph 4
The reason that ion cyclotron waves are seen primarily in the dusk local time sector is that the ring current ions penetrate into the dusk bulge region of the plasmasphere. The higher thermal plasma densities lower the resonant energies and allow ring current ions to amplify EMIC waves in this region. If the ring current is high in oxygen content as is usually the case with very large storms then significant amplification of waves below the O+ gyrofrequency will occur. The presence of upflowing O+ beams at subauroral latitudes in the dusk sector are not required to explain these observations.

Page 6. paragraph 5.
The applicability of these cited results to the present model is unclear. Over what L values were the GEOTAIL observations made? Is it possible that they were on field lines that map to the auroral ionosphere? What were the peak energies of the O+ and H+ distributions (50 keV O+ and H+ have very similar charge exchange lifetimes)? It is not clear how asymmetry in the ENA observations of a storm by CEPPAD lend support to the storm picture that has been constructed. Please explain this statement further.

Referee B

Referee report on GRL ms. 6841: "A new magnetic storm model," by Sheldon and Spence

This letter displays some very interesting energetic particle data sampled by the POLAR spacecraft, concerning the storm-time ring current particle distributions and dynamics. A presentation and discussion of this data is certainly suitable for a special GRL issue on results of WIND/GEOTAIL + POLAR. However, as discussed below, I believe that the authors run into considerable trouble in their model interpretations. I therefore cannot recommend publication of this letter in its present form.

Unfortunately, the most basic premise of the proposed interpretations does not make sense. The authors state (e.g. see the abstract) that the injection of a fresh population of ions with a "trapped" pitch angle distribution (the nose ions at ~90 keV) without accompanying fresh electrons (they cannot penetrate to these L values) generates an electric field that further confines the ions to the magnetic equator and accelerates electrons into the ionosphere. Perhaps I am being dense but it is quite obvious to me that the injection of these fresh ions will have exactly the opposite effect. To the extent that any appreciable parallel electric field is generated at all, the electrons will be accelerated towards the equator. Thus, the authors entire premise seems to fall immediately apart.

The "field-aligned" ion component has been reported previously in the literature, and these data must be discussed in the context of previous findings. Figure 1 makes it clear that in fact these are not "field-aligned" but are the so-called "butterfly" distributions. The authors should see Sibeck et al. (in the book MAGNETOTAIL PHYSICS, edited by Lui, 1987) and Sibeck et al. (JGR, 1987, p. 13485), where an explanation of these butterfly distributions has been proposed.

The conclusion that a 30 keV magnetic field-aligned potential is generated in the plasmasphere is astounding and not believable. Since the data are open to many interpretations, only a solid theoretical development proving that such fields are allowable in the plasmasphere would convince the reader that such parallel potentials can exist. To do so, a complete potential profile extending from the equator to the ionosphere must be derived for the reader from the Whipple or other works. Alternatively, the authors may speculate about the POSSIBLE existence of such fields, but they may not claim that their speculations are grounded in theory.

As a minor point, the distributions have reasonably broad widths in energy, and thus they are not "monoenergetic". A better word should be found. Also, there are published work on PC1 waves associated with the oxygen gyrofrequency. The authors do not need to rely on unpublished work.


Our E-mail Response

Date: Tue, 3 Dec 96 17:00 EST
From: r*sheldon@bu.edu
To : grl@swri.edu
Subject: to Hunter Waite re: manuscript #6841

Dear J. H. Waite, Jr.,

We knew that the paper we submitted to GRL would be controversial, we had a lively discussion at the Huntsville Workshop where we first presented it. We were both challenged and encouraged by the response we received. But what we did not expect from GRL was the complete lack of interaction, the rejection without rebuttal, presumably because of private (cover letter) communication with the editor, since we did not detect complete rejection in the referee reports. To quote, "Therefore I must conclude that this paper is not converging toward publication and that further handling of it in its present form is not warranted." In the usage of physics, "convergence" is an iterative motion towards a solution. There has been no iteration allowed, and therefore, a priori, no convergence.

Since we have been summarily judged and found wanting, please permit us the opportunity of judging our referees. Referee A uses as his major objection, the fact that:
"(The Dst, which was not shown in the paper, decreased to -48 nT over a period of a few hours then recovered rapidly within a few hours. The asymmetric component of the Dst decreased to nearly -200nT during this same interval and rapidly recovered.) How does one construct a magnetic storm model on the basis of data taken during this very weak perturbation in Dst which does not really appear to be a magnetic storm?"

On the surface this is an impressive dilemma. But one should look a bit closer. Dst takes about 3 years to appear. This was April 15, 1996, only 6 months ago. Where is this referee getting his Dst? The answer is that he is NOT getting Dst, but a computerized substitute, DSY, generated automatically by a program at Kyoto that came on line in August, 1996, which to our knowledge has never been compared to Dst. Furthermore, the reason Dst takes 3 years to come out, is because Sugiura manually removes the ionospheric component, Sq, from the magnetograms, a difficult task that he feels precludes a computer algorithm. The month of April had a week with DSY above 20nT POSITIVE, a quite hefty Sq contribution. Thus we do not include DSY because it is clear to us that it is contaminated, untested and unproven. But what does this referee's assertions about Dst show? It shows that he is speaking about a subject that he has superficial knowledge of, yet the editor feels his criticism to be so severe as to preclude any reply from the authors.

Let us continue. Referee B gave a single page response. The crux of his criticism is:
"Perhaps I am being dense but it it is quite obvious to me that the injection of these fresh ions will have exactly the opposite effect. To the extent that any appreciable parallel electric field is generated at all, the electric field will try to push the ions away from the equator, and the electrons will be accelerated towards the equator. Thus, the authors entire premise seems to fall immediately apart."

We beg to differ, perhaps the referee is being intentionally dense. We cite in our paper, which is far too brief to rederive all the well-known results of the field, one of the seminal papers in the field of parallel electric fields, Elden Whipple's 1977 JGR classic. In that paper, Elden plots exactly our electric field. Now Elden does plot the field for a beam of electrons, which we replace with a beam of ions, but the shape is invariate, pointing away from the equator. Clearly the referee's intuition has never been contaminated by reading the literature in the field or our careful citations.

This ignorance on the part of the referee is reparable, but the second criticism reveals a more profound and possibly irreparable difference. He says:
"The "field-aligned" ion component has been reported previously in the literature, and these data must be discussed in the context of previous findings. Figure 1 makes it clear that in fact these are not "field-aligned" but are the so-called "butterfly" distributions. The authors should see Sibeck et al. (in the book MAGNETOTAIL PHYSICS, edited by Lui, 1987) and Sibeck et al. (JGR, 1987, p. 13485), where an explanation of these butterfly distributions has been proposed."

It seems curious to us that such a positive identification could be drawn from the color contour spin sector plots provided in our manuscript, which contain little information as to pitchangle, whereas the Sibeck paper referenced above defined "butterflies" in terms of pitchangles. More revealing is the fact that one of us was a severe critic of that same identical 1987 paper. Could it be that this referee, unknown to the editor, has an axe to grind concerning "butterfly" distributions, a bias that might impair his impartial reading of our manuscript? Without allowing us the privilege of a response, the editor could be falsely led to believe that the credentials of the authors are somewhat less reputable than the referees.

Now we ask you, should a carefully reasoned and written paper be summarily executed by anonymous referees who can so "obviously" dismiss it with their inerrant intuition? Should there not be an opportunity for us to defend ourselves against such condescending treatment? Isn't GRL the right forum for innovative ideas and new results? If not GRL then where can one publish creative thinking? Is it in the best interests of the editor and the journal to avoid the normal refereeing give-and-take? What then is the difference between anonymous refereeing and ambushed assassination?

Sincerely,
Robert Sheldon
Harlan Spence


E-mail from GRL

Date: Tue, 3 Dec 96 17:11:48 CST
From: grl@swri.edu
To: r*sheldon@bu.edu
Subject: re: to Hunter Waite re: manuscript #6841

Dear Dr. Sheldon,

Thank you for your e-mail message regarding your paper, "A new magnetic storm model" (6841). Your point about the inappropriate use in our letter of "convergence" is well- taken. Indeed, the phrase you cite is normally used in rejection letters sent to authors of papers that have gone several rounds with reviewers. I suspect that it remained in our form letter as residue from earlier correspondence. For the record, the text of the letter that should have been sent to you follows:

"Enclosed are two reviews of your paper. As you can see, there are a number of serious concerns that preclude publication of the paper in its present form. Because it appears that a substantial reworking of the paper would be required to render it acceptable for publication, we will consider any new treatment of this subject that you may choose to submit as a new paper with a new received date and manuscript number."

This is our standard rejection letter, sent when there appear to be very serious problems with a paper. Please note, however, that it is the paper "in its present form" that is being declined and that the possibility of your submitting to GRL a "new treatment" of your subject is not ruled out. Moreover, the decision to treat such a new version as a new paper with a new received date etc. is not an irreversible one. An editorial decision can always be appealed, and we are open to such appeals (up to a certain point, that is). Thus, if you feel that you can satisfactorily address the reviewers' concerns through the appropriate revisions and/or rebuttal of their arguments and wish to submit a revised version of the paper for our further consideration, you may certainly do so.

We would, of course, send the revised paper to the two original reviewers for further evaluation. However, we would also consider soliciting the opinion of a third reviewer, if you believe that the original reviewers have not evaluated your paper objectively.

Sincerely,
Bill Lewis (for Hunter Waite)