This article attempts to formulate steps towards a new strategy of magnetospheric exploration. It appears in Eos, since that is the main communication focus for Space Physics and Aeronomy. If the details of the discussion seem rather technical to readers from other AGU sections, they should instead look at what is being attempted, and consider whether a similar reevaluation would also be appropriate in their own fields. Perhaps some already have ideas in that direction, and might consider presenting them in Eos in a similar format.
Careful examination of research strategies is particularly important in space research, because of the high cost of satellite missions, both in dollars and in time and effort spent on their preparation (a similar but much more thorough examination for astronomy was carried out by Harwit ). For instance, the recently launched "Wind" and "Polar" started out in 1978 as parts of the "OPEN" project and have cost hundreds of millions of dollars. Because of this high cost, missions are few and far between. Each one therefore should to be carefully oriented to address significant and well-posed problems.
Because space missions are so expensive, space science depends entirely on public funding, and it is important for the public to feel that this work is fruitful and produces significant new understanding and discoveries. Therefore any overall strategies should consider the presentation of our work to the public and to Congress, e.g. how it can attract the public attention (the way the striking images from the Hubble telescope do), and to what extent the end of the cold war affects the rationale for space research.
That part deserves a separate article and is not addressed here. Instead, the focus is on our community's internal plans, on a strategy to make our research serve best our own declared scientific goals. While fashions and fads have a strong effect on the public's support for space exploration, a solid scientific foundation and tangible progress seem to have central importance.
Looking back to the past, one can roughly quantify such progress by "textbook level" discoveries, the ones expected to figure significantly in texbooks written 50 to 100 years from now. A tentative list of such discoveries appeared in a draft of this article, circulated for comments (Stern ; A somewhat comparable list by Harwit  is discussed at length in chapter 2 there, occupying about a third of his book). The list suggests that the rate of progress and discovery has slowed down in the past 15 years or so, another compelling reason for reevaluating the way our research is conducted.
To be sure, some of this slowdown (not all of it) reflects the maturing of our field, leading to a different perception to what constitutes discoveries. In early days [Stern, 1996], the basic features of the magnetosphere were uncovered. Each time a suitably equipped satellite went through a new region--radiation belt, magnetospause, bow shock, plasma sheet, auroral oval--a new discovery was almost unavoidable. By now satellites have visited most regions and have sampled most phenomena: the problem is to understand them, to find what makes the magnetosphere tick, a much harder task.
Perhaps one reason our missions seem less fruitful is that they have not adjusted to this change: most still focus on localized observations, generally by isolated spacecraft, and stress "going out and getting the data" with only general ideas of how those data will be applied to definite problems. There is also too little attention to the underpinnings, to the consolidation of our knowledge. This analysis will focus on three issues related to the above.
Our physics problems need to be explicitely defined, and our strategies in addressing them should be spelled out. In recent years goals have often become blurred, e.g. one mission defined its objectives as "the flow of plasma, momentum and energy from the solar wind to the magnetosphere and from there to the ionosphere and magnetosphere." True words, admirable goal, but how exactly does one design missions for this task?
Below is a "strawman list" of 25 goals which can serve as focal points to magnetospheric research (no doubt that list can be extended). In future textbooks, 50-100 years hence, the solution of any of them would probably be rated as an important contribution.
Problems associated with the plasma sheet:
Problems related to the magnetospheric boundary:
Problems of the inner magnetosphere and aurora:
It seems that most significant observations possible with isolated satellites have by now been made. Observations of the global magnetosphere, however, are synergistic: simultaneous data from several strategic locations can be much more valuable than the sum of such data taken separately.
Indeed, much of the information needed for further progress cannot be obtained otherwise. Consider the geotail: The density and temperature in the plasma sheet vary continuously, but can we tell how at any time they vary with distance down the tail or across the tail? And when a satellite in the plasma sheet observes great variations of B, n and T--does it mean the tail is flapping, or is its thickness pulsating, or dooes its profile change?
Around 1977 or so the field was probably ripe for a transition to a network of satellites, and maybe ISEE 1-2 were meant to be the first step. "Cluster" and "Interball", each involving four spacecraft, may also help, but most questions require a much more extensive network. Instrumenting the "Iridium" network of 77 planned communication satellites was one approach towards such a network. Another possibility would be a "Profile"2 mission, in which a pod of 6-10 identical satellites would be launched into a near-equatorial transfer orbit with an apogee of (say) 20 RE. The satellites would be flat cylinders, stacked on a common axis in the dawn-dusk direction and spinning slowly and they would carry magnetometers, electron and ion detectors, the latter also configured as driftmeters. At each of the initial perigee passes, one satellite would be detached and given (by a small rocket) 50-100 m/s extra speed3, so that the pod would become scattered at equal distances along a slightly longer orbit, like the fragments of comet Shoemaker-Levy just before they hit Jupiter.
Such a "Profile" mission might help time the spread of substorm disturbances and identify their origin; by straddling the region where reconnection allegedly occurs, it might also provide a better idea of what takes place there. It could confirm dispersion-free energization and time its occurence at various distances, and it might track the extent and motion of bursty bulk flows. On the day side it could relate variations of B in the solar wind to those in the sheath and magnetosphere, trace and time the erosion process and follow the progress of waves. It could also trace flank motions and relate them to sheath variations.
Alternative"networks" could also be proposed. Each observing satellite may be very simple--like a PC, not a mainframe--a magnetic vector every second, even only every 10 seconds, plasma density, simple fluxes at several energies, simple bulk flow information. It should however be durable, so that as more are launched, the network will grow, and many of them are needed, to properly cover global behavior. This may well mean proven designs rather than state-of-the-art ones: the real technological challenge comes on the ground, in devising a computer system that will properly assimilate such multi-point data.
Strengthening the Foundation
Finally, there is the task of consolidating and transmitting our knowledge. Here our community has been like an army pushing hard at the front but neglecting its supply train. It is not easy for a young scientist entering the field, or even for a veteran, to acquire a synoptic view of magnetospheric physics: thousands of technical papers exist but few useful reviews, fewer good texts, and not many opportunities to learn the material in an ordered way, such as courses or summer schools. As a result, the foundation is often weak and most workers end up knowing mainly their narrow specialities.
Furthermore, our field sometimes seems to go around in circles. Take the substorm. An enormous number of papers discuss it, yet rather little is agreed on. Does a near-earth neutral line exist? Is the ionosphere the key? Or some "current disruption"? Or a thermal catastrophe? It is high time we try to figure out what we know for sure, and what sort of observations are called for.
The situation on FTEs is somewhat similar, and even where appreciable progress exists, as in auroral acceleration, it has never been properly put together and spelled out. Many of the younger researchers are only aware of bits and pieces, usually work published after they entered the profession, not before. Spot checks are illuminating: how many are familiar with the Dessler-Parker-Sckopke theorem ? With quasi-neutral electric fields of [Persson and Alfvén, 1963]? With the injection boundary ?
Transmitting such a "core knowledge" (as well as the essential "core technology"), in writing and perhaps in summer courses devoted to the task, will go a long way towards revitalizing our science. This is not a substitute to discovery, but it lays the foundation. Among other things, just the process of trying to decide which conclusions are firm and which are not often brings new insights. Anyone who has compiled a review article would agree that just the process of trying to fit everything into a coherent picture can uncover new angles.
In conclusion, this is but a first stab at an elusive subject: now let others pick up from here and continue the process.
Acknowledgments: The author thanks Eos SPA editor Jim Horwitz for his tireless efforts, as well as the ten official referees and those SPA members who commented on the initial draft.
Harwit, M., Cosmic Discovery, xi + 334 pp., Basic Books, New York 1981.
Stern, D.P., Problems of Magnetospheric Physics (initial draft of this article, circulated for comments), AGU Electronic newsletter, 22 December 1995.
Stern, D.P., A brief history of magnetospheric physics during the space age, Rev. Geophys. 34, 1-31, 1996
1 The submitted title was "Problems of Magnetospheric Physics," but the editor insisted that by the rules of the journal, every caption had to contain a verb.
2 For a later development of this concept, see here. See also "Systematic Identification of Preferred Orbits for Magnetospheric Missions: 2. The "Profile" Mission" J. Astronautical Sciences, 2002.
3 This was an offhand estimate and turned out to be far too large: no more than 3-4 m/s were enough to do the job.
Author and Curator: Dr. David P. Stern
Mail to Dr.Stern: education("at" symbol)phy6.org
Last updated 5 April 2003