What are the objective/needs for new theoretical work on E and F region plasma instabilities and electrodynamics?
University of Saskatchewan, Canada (email@example.com)
The first goal of plasma instability theories is answer the very basic question: “What are the instability mechanisms responsible for the production of the irregularities that we observe?” At first sight, the generic answer is deceptively simple and based on the various ways by which the plasma can be made to depart from equilibrium: in this regard, currents and density gradients have been the foundations for many successful theoretical explanations of observed ionospheric irregularities. Theorists have also rightly pointed out that thermal gradients, shears, and even non-Maxwellian ion velocity distributions can all destabilize the plasma. Studies combining several of these processes have also been published. In spite of this, however, we are faced with a general lack of endorsement for these processes. Ironically, in spite of all these general theoretical studies and in spite of many ingenious proposals for instabilities, some irregularities, like the so-called low latitude “150 km echoes”, are basically not understood. This leads me to the thought that the first challenge for theorists is to make their theories “more relevant”. When exploring new mechanisms, we should look much more closely at all possible constraints from the observations so as to make convincing cases for particular mechanisms. Theorists should also have some brainstorm sessions together and with experimentalists to solve riddles like the 150 km echoes. It’s all about relevance.
The second challenge is not new but remains important and needs to be pursued as vigorously as ever. I refer of course to the need to understand the nonlinear evolution of instabilities, particularly in situations for which we know the linear excitation mechanism. This need is once again triggered by the observations, which are strongly biased to large amplitude structures and therefore often require nonlinear theories. The nonlinear work is important because it is linked to a fundamental practical application of irregularity studies, namely, their capability to tell us something about the medium (for instance about the plasma drift). The nonlinear problem goes well beyond the linear one, which simply tries to figure out the basic feedback mechanisms that lead to instability. It addresses the actual properties of the structures once nonlinear processes associated with large amplitudes have contributed to the evolution of the system. For instance, the Doppler shift of E region irregularities is still a subject of debate. In this instance I also would suggest that we have another look at observations and consider the possibility that we no longer just see only structures that have reached their saturation amplitude when we do sophisticated interferometry based observations. The smaller amplitude echoes may well have properties that differ by being more “linear-like”. Another application of nonlinear studies pertains to the general shape of F region spectra: we now have convincing evidence that the spectral width at HF frequencies has a distinct morphological signature associated with magnetospheric boundaries. Indeed it is sometimes forgotten that the spectral shape offers some very important clues: a very narrow spectrum has to be associated with weak turbulence, that is, with a slowly growing condition. We should not use power to determine the degree of turbulence, but rather we should use the spectral width. Therefore, when we look for theoretical descriptions, we should perhaps pay attention to the fact that in some cases we have strong turbulence (wide spectra), and in other cases we have weak turbulence. In the latter instance, we might want to consider whether or not a nonlinear theory is really needed. At the very least, weak turbulence should suffice. Be that as it may, we have another challeng to face: nonlinear systems offer yet another challenge in that they can trigger new instabilities nonlinearly. Neat examples of this are the trigger of m-size irregularities in the equatorial electrojet through much larger scale gradient-drift structures. At high latitudes we also have the example of Langmuir turbulence having been proposed as a trigger mechanism for large amplitude ion-acoustic waves. And finally, we must include non-local effects in the nonlinear category. What do people make for instance, of the fact that an “eigenfrequency” would in principle be a function of space? There are ways around that contradiction but they all involve nonlinear work of one form or another.
A third challenge is to figure out the role that the irregularities play in the system. In the long run, this has to be the most important challenge. But, it’s also the most difficult. With this challenge we address the fundamental issue of the plasma instabilities: if they are created by a lack of equilibrium, this also means that their role is to bring the plasma closer to its equilibrium, somehow. If currents are the trigger, then they should somehow weaken. Likewise if density gradients or shears are the trigger, they should be weakened by the instability. This brings us to the calculation of anomalous transport coefficients, which, to my taste, is still often an art more than a science. That’s partly because we have too few constraints to go by. However, every once in a while the plasma gives us useful clues that we can work with. For instance, the current profile in the equatorial electrojet gives us clues about the anomalous resistivity, while the electron heating in the high latitude electrojet gives us a wave heating rate and tells us about the importance of parallel electric fields in the nonlinear evolution of the structures (interestingly enough, in a modified two-stream instability, one way to stabilize the plasma is indeed to heat the electrons). The third challenge, in other words, is to quantify the anomalous transport coefficients that would allow us to properly adjust the global properties of the plasma through proper effective transport coefficients. This is not easy: sometimes we cannot even seem to agree on the processes that control the nonlinear evolution, as exemplified by the debate that took place regarding electron heating at high latitudes, with one school of thought pushing for anomalous diffusion while another favoured parallel wave electric fields.