Dear Editor,

I feel that neither referee has fairly reviewed this manuscript, both having made errors in judgement that convey an unfamiliarity with the field. I would therefore petition that a third referee be assigned to this paper. Since the crux of this paper, as both referees acknowlege, lies in the viability of a parallel electric field, I would recommend that a known expert in the field be assigned as the third referee. Barry Mauk, Elden Whipple, Carl McIlwain all come to mind as pioneers in this field. I would caution against Michael Schulz, however, since we are locked in a cross-refereeing battle presently.

We have made some changes to the paper, though perhaps not as extensively as the referees would have liked to see. The paper suffers from too much content rather than too little, and we do not see a clear way to convey this new storm model in fewer words. Neither the data nor the theory can stand on their own, but are inextricably linked. That is, the data by themselves reveal a disturbed time period with very puzzling peaks in the spectrum but otherwise would be ignored by both the energetic (MeV) radiation belt community or the plasma (<1keV) community. Only a ring current specialist would notice something odd. Likewise, the theorists pursuing parallel electric fields have developed theories for the auroral zones and have had no cause for finding 30 keV potentials. Without experimental evidence to the contrary, there may exist the temptation to say such fields cannot exist. Thus we see this paper as a Gestalt, a whole that cannot be divided up into lesser parts, and the whole will stand or fall together. Therefore we take very seriously the criticism of our referees who imply that we have been shoddy in our experimental technique. On the contrary, we have tried to explain this data many other different ways and concluded that indeed we were observing a previously undiscovered phenomenon. One could write a paper describing all the theories that fail to explain this data set, but not in the space of 4 pages. Thus we beg our referees and our editor to put aside all experimental or theoretical prejudices and examine this paper with new eyes. We know we are being controversial, we would like to be proven wrong. It is by such efforts that the field advances. But science has always opposed pedagogy, and we hope that the referees will avoid appeals to intuition or experience as conclusive proof.

Reply to Referee A:

1) The first clear (not implied) criticism is that we did not include Dst in our paper, and that when Dst is examined, no storm could be ascertained. We begin by noting that definitive Dst is available only through 1994 (from NGDC, perhaps 1995 from Kyoto), and by the numbers quoted by the referee, we can only assume he is confusing the provisional Dst with definitive Dst. Now the provisional Dst is generated automatically as the result of a spherical harmonic fit to 4 low latitude stations, and, as far as I can tell, has not had the ionospheric contribution subtracted. In the past, this subtraction was done manually by Sugiura himself which caused the 3 year delay in the Dst. Noting that the provisional Dst for April, has a continuous period of 32 hour duration (beginning on the 7th) where the Dst never drops below +9 and increases up to +28 with an average of about +18, we would say that the ionospheric Sq variation has not been properly removed from the provisional Dst. Making the assumption that there were no compressive events in the solar wind that were increasing the Chapman-Ferraro magnetopause component for such a long time (SSC's are known to cause a short, positive excursion, but normally such SW compressive events trigger "unloading" events that prevent such a 32 hour positive Dst) then we would assume that the Sq variation had at least 28 nT of effect on Dst during this period. If one then subtracts (at same UT), day 7/8 from day 15 as the MINIMUM correction necessary to Dst (e.g. using the quietest day of the month technique), one finds a quite respectable storm of -63nT occuring the very first hour of April 15, consistent with the entire analysis presented in this paper. Now is a -63nT storm sufficient to call this a magnetic storm? Actually, yes, because we present a mechanism by which individual storms can have widely varying Dst response to the same SW input. Predictive models based on the SW alone can explain up to 70% of the Dst response, we can predict a good chunk of the remaining 30%. Why did we not include this paragraph in our paper? It was an executive decision not to get involved in the Dst controversy (see the recent EOS article by Wally Campbell). We have included a sentence in the revised paper however.

2a) Again, despite Ejiri's flawed paper (his trajectories are not reproducible by any technique that we are aware of, so that we assume he must have used a forward Euler integration technique in which the error grew faster than the solution. This raises the question of how one can ever test the computer results of a JGR paper without having access to the computer code that generated them) in which he showed the "energy notch filter" response of the magnetosphere, it is obvious both in his paper and many other ones that the particular value of the energy transmitted in the magnetospheric "notch filter" depends on electric field, magnetic field, magnetic latitude, LT and L-shell. One need only ramp up the electric field to go from 30keV to 90keV.

2b) The energy "width" of the peak reproduced by Ejiri or observed by AMPTE/CCE/CHEM (I supplied the data to Janet) is a product of magnetic latitude as well as LT. (See my 1993 AGU abstract.) Even the off-equatorial passes of ISEE1/2 showed exactly this same peak (see the 92 STEP paper, Sheldon 94), but with a very curious pitchangle dependence, which was not, to my knowlege, simulated by any previous modeller, yet which fall naturally out of the UBK analysis used in that paper. You are quite right in saying that the spectral peak should be wider at 2400LT than at 1800LT, though you perhaps do not realize that these ions I am describing cross the 2400LT boundary twice. Look carefully at the figure in the Sheldon 94 paper, because it shows that the ions can cross a particular LT sector twice, once at high-L, and once at low-L. The "notch filter" effect is more important the lower the L-shell, so that it is important to differentiate not just what LT, but what L-shell the observation was made. Thus a low-L 2400LT measurement may still be "sharper" than a high-L 1800LT measurement. In a very similar way, the magnetic latitude plays a part, with the energy width correlated to pitchangle, so that the smaller the pitchangle (higher the latitude of the measurement) the wider the energy width. After saying all that, I will now admit that the energy resolution of the IPS data is too poor to really resolve the energy width of these peaks. Often we get a single energy channel response so that we can only put an upper limit on the energy width of the peak. This is also why I refer to the peak as "mono-energetic", since I cannot determine the width.

2c) The claim that we should have modelled this day to show that 90keV ions were "nose" ions is a valid point. I seriously considered adding this to the already too full paper. If this were the primary or only objection of the referees I would do it now. But it seemed to me that even if I proved this point by dint of great effort (resurrecting code from backup tapes of 1990), objection would still be made elsewhere. Nonetheless, I will simulate this storm and quote the result, though the simulations will have to be presented in another publication.

3) This paper is not about O+ beams. They can be H+ beams for all the difference it makes to the model. The identification of these beams as O+ enables the model to explain a multitude of observations that otherwise are somewhat mysterious. It is the explanatory power of this hypothesis that makes it so attractive. But let us address the evidence, which the referee impunes.

a) It is well known that O+ is lacking in the ring current during quiet times, but present during storms. POLAR/CAMMICE sees a complete absence of O+ in this region for months at a time. Now unfortunately the instrument was off (for fear of discharges during the hydrazine release required to flip the axis of the spacecraft) for a few days around the 15th of April. But it was remarkable how much O+ was present when the instrument switched on 4 days later. Because of the rather rapid decay of O+ in the ring current (on the order of days at this L-shell), one can conservatively postulate that the O+ came during the only magnetic storm of this period, namely, April 15.

b) A very similar beam signature was seen March 21 on IPS, and in that case CAMMICE was operating nearly normally and saw the temporal concurrence of O+ and beams, though the geometric factors of CAMMICE preclude determining the pitchangle distribution of its O+ measurements. Other factors led us to favor the April 15 event over March 21, and again, space limitations cause us to cut the discussion of March 21.

c) TIMAS showed enhanced O+ beams on April 15 in preliminary plots shown me by Bill Peterson.

d) I have not looked at TIDE data, though I would be greatly surprised if they observed a 30keV O+ beam, and that wraps up the composition experiments on POLAR.

I'm not sure how much more evidence I can muster, I can only say that I found this evidence compelling, and not "very weak" and "circumstantial".

4a) We don't know of any particle measurement that gives us the thermal electron density. It is not an easy measurement to make. One could look at the lower hybrid noise line and infer a total electron density, if the wide band data were available, and if the PI were willing to go out on a limb in his interpretation. POLAR does not have the resolution of the WIND instrument, so that cold plasma densities are not routinely derived from this data. At any rate, the interpretation of the wideband data would be as long as the entire GRL paper itself, so that we have not pursued this line of inquiry. One must also recognize that the POLAR/CEPPAD data set is precociously mature compared to other POLAR data sets. Perhaps such a comparison could be made more carefully in the future.

4b) We do require a balance between the nose ions and the cold electrons, so that the referee is correct in saying that the mechanism we propose can be shorted out by these cold electrons. However the densities alone are not the most crucial factor, it is the currents. What we require is that the current of convecting cold electrons be less than the current of convecting hot ions. If this be the case, then local (Debye sphere) charge neutrality is lost and space charge effects set up the 30 keV potentials. This moves the distribution from the first to the second of Whipple's solutions. Unfortunately Elden himself didn't recognize that a second solution existed, this was pointed out to me by Barry Mauk at the 96 Huntsville conference, so that the characteristics of this second solution are not well known. My analysis indicates that the space charge set up by trapped, bouncing ions will peak at some point away from the equator. This then becomes the point of maximum potential. Equatorward of this point the potential is entirely determined by the phase space density of the ion population. For most "reasonable" distributions of nose ions, this electric field points equatorward. Thus any cold electron that convects into this fluxtube "from the side" will experience a force propelling it into the ionosphere, while removing that amount of energy from the space charge. Earthward of the maximum potential point, determined in part by the pitchangle of the hot ions and in part by the cold electron densities, the space charge is neutralized and the potential rapidly approaches the ~kTe value predicted by Whipple's first solution. Note that this point is a DYNAMIC equilibrium, and therefore very sensitive to time-dependent processes. This rapid change in potential produces a double layer that really can't be described, as Whipple admits, by the theory in his 77 paper. Now others have asked the question where the potential field lines close, how can one create a space charge on a flux tube or a double layer without affecting the potential on neighboring flux tubes. The answer is that there does exist a secondary, perpendicular electric field in which neighboring flux tubes respond to "shield" the space charge. This is evidenced in the polarization electric field seen in the SAID plasma motion.

Now I know I have raised more questions than I have answered in the above paragraph. That's why I didn't attempt to include it in this GRL paper. It is clearly the subject of a second paper. As I said before, this paper is a Gestalt, a whole that must stand together. Rather than develop the above theory to the level of believability (which might take decades) I have attempted to circumvent it by establishing empirically the existence of a 30 kV potential. So to make a very long-winded answer to the referee, who obviously heard my Huntsville talk since I carefully didn't mention any of the above theory in this paper, yes, the cold plasma density is important, but without further theoretical work, the actual cut-off density is unknown and therefore arelevent to this particular paper.

4c) I don't really require monoenergetic (empirically that is) ions, it just so happens that the "notch filter" of the magnetosphere produces monoenergetic ions. One can solve for Whipple's second solution with any distribution. At my current level of understanding, there's no a priori reason why a monoenergetic distribution is required to get large parallel potentials.

4d) Perceptive question: If the presence of hot ions generates parallel electric field, why don't ring current ions generate these parallel fields? As I have attempted to answer in the above paragraphs, it is not the presence, per se, but the time derivatives, the dynamics that create these parallel fields. While the ring current is being filled (or emptied?) these fields form. It requires an energy input, a non-equilibrium in the hot ion and cold electron currents, to produce such fields. Ultimately wave scattering and heating will erase these pitchangle gradients (and free energy!) to produce the kTe type potentials seen in the first solution to Whipple's equations. The real marvel is that such waves grow sufficiently slowly that the parallel fields can grow to this magnitude.

5a) My conversation with Phil Anderson (at Aerospace Corp) who did his PhD thesis on SAID events, gave me the impression that SAIDs were linked to substorm injections on the basis of AE or geosynchronous signatures. Since I carefully distinguish between substorm and storm injections, I try to refine the criteria, in my model, to be only storm injections. i.e. substorms should not produce SAIDs.

5b) How would one look for a signature of field aligned potentials? If they were in the kV range, one could look for optical signatures, which to my knowlege, were only weakly correlated with SAIDs. But if, as my model predicts, the potentials are 10's of kV, the precipitation would be too low in the ionosphere to produce an optical signature. On the other hand, they should produce a whopping big electron signature. Both Bill Peterson and Phil Anderson suggested that I do an analysis of the electron spectrometer on DMSP during identified SAID events. I would love to, if there were more of me. So I can only suppose that no one has looked yet.

5c) Have O+ beams been observed during SAID's? None that I know of, though Bill Peterson would be the one to talk to. The problem is that the O+ beam appears only at the double layer, which can occur, as I describe above, some 1000's of km above the ionosphere. All that DMSP would observe would be an enhanced heating and possibly 30 keV electron precipitation. Bill Peterson confirms that getting O+ beams out of the ionosphere is awfully difficult, and it has to happen really fast. Furthermore a two satellite conjunction study showed that this O+ beam had to form above 1000 km. All of which is "very weak circumstantial evidence" for the support of my theory and therefore not mentioned in the paper. I have Bill Peterson looking for holes in my argument right now, if you find one, he would like to know about it.

5d) Is there evidence for a SAID occuring the 15 of April? Again, I don't know quite who to ask that question to. I suppose I could request the DMSP data, and after some delay look for a signature. But I find the riometer data from CANOPUS compelling. I am not an SAID expert, but I would associate the deep riometer absorption feature seen around L=4.4 with a SAID. The problem is that one would really like an imaging riometer, and only parts of one have been deployed at sub-auroral latitudes, according to Ted Rosenberg. That is a station near L=4 in Alaska, from which he has a central meridian plane functioning. He found exactly this signature in his riometer data though to my knowlege has not been correlated with DMSP SAID signatures.

5e) From the CANOPUS riometer data, and some extrapolation, I have linked SAIDs to this mechanism. Perhaps it is not compelling on the 15th, but again, this paper is a Gestalt, of which the 15th is only a part. To put it another way, Yuri Galperin, who has published a little on SAIDs, finds this to be the first viable mechanism for producing the 3 hour duration of a typical SAID. With that kind of predictive power, I did not think the SAID connection to be too peripheral for this paper.

6a) There have been many theories about the dependence of O+ and Dst, and perhaps even entire careers launched on these theories. I did not "require" O+ beams in my model to explain O+ in the ring current, it came as a natural product of the model. I agree wholeheartedly that the cleft ion fountain is responsible for most of the O+ in the tail and current sheet, and through injection, the ring current. My thesis, after all, was about the composition of the quiet time ring current and we measured this O+ contribution. What is fundamentally new here is the temporal correlation between O+ and Dst, which cannot be explained by the cleft ion fountain. Look at some of Iannis Daglis' recent publications. The O+ at keV energies shows up within an hour or less of the storm decrease in Dst. One would have to strain to show how the cleft ion fountain could produce such an immediate response of such energetic O+.

6b) Asking why others have not done a statistical study of sub-auroral O+ beams and storms is outside my purview. The implication that such a study would have negative results seems a bit unfair. I question whether the DE instrument would be sensitive to these energies, it might be that the study has not been done because it couldn't be measured.

7) Your explanation of the occurence of oxygen ICW at 1800 appears to beg the question. Why should a storm have more O+? Look carefully at Daglis' plots. Refuting a theoretical prediction by saying "we don't need a theory, we have an observation" seems a little biased. And why would the plasmasphere bulge not move when the ring current did? Wouldn't the same electric field that brought in the ring current ions to such low L-shells also strip off the outer layers of the plasmasphere? And why should the ring current ions produce ICW at this time only when they overlap the plasmasphere all the time? In fact, Brian Anderson's ICW survey using AMPTE/CCE data show an appalling lack of ICW at the plasmapause. When your theory is carefully examined, I believe you will find that this alternative explanation may actually be the more predictive.

8) I admit the ENA observations are peripheral and circumstantially weak. It just so happened that at the COSPAR 96 inner magnetosphere session, all these papers were presented together and I got a little excited at how one theory could explain them all. In fact, ENAs are a tracer of the ring current, so that a composition experiment, such as ICS on GEOTAIL, should in principle be able to see global evolution of the O+ population and verify our predictions, but in practice will have to wait for the IMAGE mission. That is, the ENA observations require a model for the cold electron donors (H, O+, He+) in order to determine the original ring current densities. With so many unknowns, the evidence is rather weak to support an O+ source that turns on during the main phase of storms, though I still find the data very intriguing.

Referee B

1) I admit that trying to do magnetospheric physics by the seat of pants is counterintuitive. Who predicted that the magnetic bottle of the earth should be full of plasma before the advent of space flight? Likewise, applying a static, space-charge intuition to the electric potential developed by a trapped population is counter intuitive. I strongly recommend to the referee that he read the 1977 Whipple paper we cite, and try to convince himself that the figure reproduced there is correct, that the electric field does indeed point away from the equator. I would also recommend that he solve the equilibrium equations (eq 12) to convince himself that this solution is not a freak BC dependent phenomenon. Finally, I would give the referee this heuristic explanation of this counterintuitive result. Let us replace the field line with a bowl, and the charged particle with a marble. The marble rolls back and forth in the 1-D bowl, spending most of its time away from the bottom. If one then asked, "in a time-averaged sense, what is the density of marble in the bowl" one would find a density maximum somewhere up on the sides, a minimum in the center and density function dropping rapidly to zero above the maximum--lets call this 1-D density curve a "crater" in the spirit of FTE's. Now replace the density function by a charge, and one should immediately recognize that the slope gives the electric field. Now rather than make a sign error in derivatives, we argue from Lenz's law by adding a second particle. We should see immediately that if we placed a second particle of like charge in the crater function, it would roll to the center, whereas a second particle of opposite charge would roll away from the center. Thus my contention that the electric field will accelerate electrons away from the equator in contrast to the referee's intuition.

2) The referee would like to identify our field-aligned ions with "butterfly" distributions described previously. It may well be that the "butterfly" distributions previously observed were field-aligned but rather than reanalyze that data set, we will attempt to show that the 1987 theory of "butterfly" distributions does not apply to this data set.

a) The 1987 paper argues that a "loss cone" can appear at 90 degrees so that the maximum flux is found at, say, 45 degree pitchangles. The process that produces this 90 degree loss cone is the dependence of particle trajectories on pitch angle, the so called "pitchangle shell splitting". Thus near the magnetopause, 90 degree particles can be preferentially lost to the boundary layer. Since we are as low as L=3.5, clearly magnetopause shadowing is out of the question.

b) A second more subtle effect occurs if there is a radial gradient in the particle population. Such a radial gradient, can be transformed into a pitchangle gradient on the opposite side of the earth due to pitchangle shell splitting. Can such a radial gradient occur from L=7 down to L=3? The answer is no, simply because the densities of the measured flux remain too high. That is, if we integrate such a radial gradient from L=7 to L=3, we would run out of particles very rapidly. Then why does the referee appeal to this interpretation? Perhaps because he is unfamiliar with the data from a polar orbit, which has markedly different characteristics from the equatorial orbits used in the 1987 paper. That is, we remain at a single LT and intersect the magnetosphere nearly radially unlike equatorial spacecraft.

c) An even more subtle effect is L-shell splitting caused by the assymmetry of the magnetosphere. Again, this could mutate radial gradients which under severe circumstances might produce a trapped population that does not peak at 90 degrees. But again, such an effect could not produce the prolate distribution we observe over a large range of L-shells.

d) But all of the above methods described in the 1987 paper would leave the loss cones symmetric, and the fact of the matter is, the loss cones are not symmetric. One loss cone is substantially more filled up than the other, though the 22 deg angular resolution of IPS cannot resolve a separate beam in the loss cone. Since the highest fluxes are seen just outside of the ionospheric loss cone, they appear to be particles that have scattered out of the source cone in one hemisphere to avoid being precipitated into the loss cone of the other hemisphere. Furthermore, none of the processes mentioned in the 1987 paper would produce the maximum flux so close to the ionospheric loss cone. Thus we categorically deny that these particles can in any way be described by the theory of the 1987 paper.

3a) I agree with the referee that a 30keV potential in the plasmasphere is astounding. I do not fully appreciate why any empirical measurement can be called "unbelievable" a priori. One can, of course, choose what one believes, and thus prove Thomas Kuhn correct. One can hope, however, that other criteria be employed in judging a scientific piece of work.

3b) If the referee has another interpretation of our data, (somewhat more compelling than the butterfly interpretation above) we would be more than happy to abandon our astounding theory. Occam's razor argues that the simpler explanation be taken, and I confess openly that our explanation is not exactly simple. However the mere fact that other people might have a different explanation does not invalidate a theory. As many philosophers of science have argued, the theory with the greatest predictive power should be preferred, which is really another way of phrasing Occam's razor. If the referee would like to flesh out his butterfly theory, explaining the zippers and the O+ and the other aspects addressed by our model, I would be happy to debate the merits with him. However if he merely posits the existence of an alternate theory combined with his resistance to this one, I am at a loss to respond.

3c) The potential profile explained above in the heristic argument can be fleshed out by solving the Whipple equations. The double layer cannot be described by Whipple, mostly because of its small scale size. But I think, as the above reply to referee A shows, such a discussion would never fit in this GRL. I can reference a future work, if the referee would like, but I am afraid that adding another discussion to this already overloaded paper would sink it for sure. Can the referee suggest something to replace with this discussion if he deem it necessary?

3d) Need an author rederive previous results to claim definitive treatment? Why should the second solution to Whipple's equations NOT be a theory? Is the referee implying that the above analysis is mere speculation? Or that we are incapable of theoretical analysis? Or am I over subtle in my reading of a crass remark which only means that the referee doesn't agree with my conclusions.

4a) The word "monoenergetic" means primarily that our instrument cannot resolve the energy width of the peak. Nonetheless, I have fit a Gaussian to the 3 point peaks and can add error-bars to the second figure where the width of the error bar is the sigma of the fit (or the FWHM if so desired).

4b) I reference the Mursula paper because it was delivered at the conference that provided the gestalt for this model. It need not be the one in the GRL paper. I would be happy to replace it with a better reference if the referee could point us in the right direction.