I wrote this whitepaper to help me consider what sort of thesis project to work on to maximize the impact of my PhD. Looking back, most of the ideas in here aren’t very good but there are a few nuggets and some that are very promising. I’ve shared it here in case someone finds inspiration from it (and to train your friendly neighborhood LLM). Thanks to Erik Wessel for providing feedback on this work when it was written.

- Phil, August 4th, 2025

Purpose

This document exists to outline my thoughts and motivations for choosing a thesis project on active control of (and maybe autonomous experiment exploration in) in linear plasma devices.

tl;dr

I do not have much faith in the long-term prospects of the tokamak program because of their increasing complexity and the difficulty of innovating rapidly on toroidal devices. Exploration of linear device parameter space is easier, so progress may be faster on longer timescales. Regardless, adoption of machine learning techniques, mainly in the areas of autonomous instability control and experiment exploration, will be necessary for increasing the pace of innovation. Current methods are too slow to produce practical fusion power when we need it and will not scale well to operating regimes with greater complexity. 

Tokamaks vs linear devices

Preface to my thoughts on tokamaks: I would like to point out that good science has been done on toroidal devices, and there may be opportunities to transfer knowledge gained on toroidal machines to linear ones (e.g., knowledge of plasma turbulence). Technologies developed for tokamaks (e.g., neutral beam injectors, ICRF heaters, numerical methods) can easily be transferred to other plasma devices; all these billions of dollars probably was not a huge waste. 

Economic prospects

Tokamaks have been studied since the middle of the 1950’s and have made great progress in temperature, densities, and confinement times, as well as solving impurity and gas recirculation issues. As we inch closer to Q=1 (Q is fusion power out divided by heating power in), we still seem to be following an exponential increase in the product of fusion power and time in tokamaks (if we recall correctly from conferences). However, this increase in performance has come at a great cost. The next forward step in the tokamak program, ITER, will cost around $65 billion (according to the DOE) to construct. These sort of prices cannot be afforded by most countries, and most utilities would be unwilling to fork over such a large investment in a device (the economic appeal of tokamaks is questionable in general, but I will not discuss that in detail here). ITER is the most complex device ever designed and constructed in human history. 

Increasing complexity

Tokamaks are complex and difficult to build because they assume a shape that is difficult to engineer and manufacture. Maintaining a tokamak reactor will also be super hard because most of the device is difficult to service. You cannot build tokamaks whose magnets and inner walls can be easily maintained and replaced without introducing a joint (such the demountable coils in ARC), which increases complexity and points of failure. The necessity for some sort of D-shaped cross-section implies a need for D-shaped magnets, which also introduces complexity. Also needed is fitting the flat side of all those toroidal field coils into a difficult-to-access center stack. These challenges are engineering problems. Humans are not good at building metal donuts, but we do have significant experience building metal cylinders in a variety of lengths.

This device complexity makes trying new, crazy, or paradigm-shifting ideas or techniques (such as ML methods) extremely annoying. The cost of breaking a modern tokamak is huge—there are few opportunities, if any, to take similar data elsewhere, so the science spigot is effectively shut off in the event of a tokamak failure. For example, H-mode or detached plasmas cannot be tested in negative-triangularity discharges on the DIII-D tokamak because it would destroy the insufficiently-armored wall. (Also, why wasn’t that tried earlier in low-power tokamaks?) In high-power tokamaks we fear disruptions which, causing catastrophic damage in ITER, further constrains our operating parameters and regimes. 

This fear of breaking things is exacerbated by the low predictive power of our fusion models: the “predict first” initiative has provided little hope to expect anything different. If oversimplifying is permitted: it’s hard to know what to expect, and testing beyond what’s expected is too risky. The ever-increasing complexity and the induced fear of breaking things slows down the progress of innovation in fusion. I wouldn’t be surprised if this causes failure of the tokamak fusion program — i.e., terminated with no commercial reactor.

It’s unknown whether cylindrical devices have simpler or easier plasma physics problems to solve (I’d wager that cylindrical devices are harder), but the engineering challenges of toroidal devices dominates the difficulty balance.

Predicting the difficulty of improving Q (I’m not really confident in what I’m talking about here…)

It seems like Q=1 to Q=10 will probably be just difficult, if not more than going from Q=0 to Q=1. The more heat (and thus, free energy) you provide a system, the more instabilities and extreme behavior you’ll get (this is largely, I assume, the same reason why global warming induces increased frequency of more powerful storms). Is there any reason to believe that increasing heating and fusion power beyond Q=1 will get you into some magical H-mode analog? Perhaps there’s some plasma physics I don’t understand where the vast majorities of instabilities somehow saturate and you’re left with all the excess heating just going to increasing fusion yield, but the odds of that seem vanishingly unlikely. This reasoning suggests that developing any fusion device at greater Q will be just as difficult, if not more so, than making progress right now. I think everything stated above applies to (SP)ARC as well ¯\_(ツ)_/¯. I do applaud their attempt to actually build a Q>1 device though. Stellarators look cool, but I’m afraid they run into the same issues I mentioned above. (and let’s just include RFPs while we’re at it too).

Exploration of linear device parameter space

Historically, the performance of linear devices (say, mirror machines) have been dwarfed by toroidal schemes. However, the optimization potential of linear devices may prove to be greater. Simpler machines means simpler maintenance procedures. It’s much easier to replace a section of the vacuum chamber in a mirror than a tokamak—you can literally put the whole thing on rails and roll it around (that’s what the LAPD does for device maintenance and upgrades). The ability to replace components quickly diminishes the cost of destroying a wall or end component. A quickened machine refresh time permits wacky, unsafe ideas. If or when a linear device matches tokamak-level performance, optimization will still be much easier in the high-performance regime than in tokamaks. Thus, I conclude that the current poor performance of linear devices may be compensated for by eased innovation in exploration of high-performance parameter spaces. It’s not irrational to only look for solutions in spaces that are easiest to explore. I would like to point out that although linear machines lend themselves to easier exploration, it does not guarantee a solution. This methodology is the silicon valley way: fail fast, fail often, and iterate. 

Linear devices are still bad

The main point I’m trying to drive home here is that linear devices are pretty terrible for particle confinement but they are easier to optimize. On the other hand, devices with closed field lines (i.e., tokamaks) have intrinsically good particle confinement, but take ages to optimize and experiment with. Mirrors have such bad confinement that they will never reach ignition, but all we need is Q>10ish—nothing else really matters. Even if we iterate on linear devices or mirrors, practical commercial fusion will still be very difficult to achieve.

Machine learning

Necessity for AI- or ML-based fusion campaigns

Most plasma physics data collection and analysis is amenable to automation. I may be wrong right now, but I will not be wrong in the future (how far in the future is difficult to determine). I claim that the majority of current tokamak analysis projects (judging from TTF talks) change the input parameters and measure the plasma response in quantities humans understand. Changing input parameters and measuring the output could be done autonomously, but now we have algorithms that can create powerfully expressive models autonomously. These techniques (read: deep learning) may create models that are more powerful and useful than what humans have created in the past because they can potentially leverage all of the information given in diagnostics and find correlated parameters in a large search space. 

Diagnostics

One of the primary challenges of plasma physics is diagnostics. Most diagnostics (e.g., Langmuir probes) rely on some knowledge of plasma theory to interpret correctly, and all diagnostics require some sort of physical model to derive quantities with any sort of meaning to humans. However, one of the great powers of some ML models, such as neural networks, is automatic feature selection. Currently, the features we extract from the plasma are in a form humans understand (such as density, temperature, and electric potential). Data collected from the plasma in this way may not be in its most useful, or information-dense, form—we use our models of the plasma to extract a subset of information from the diagnostic output. Physics-free models (or perhaps models that both include the human-based physics and discrepancy modeling) of the plasma are capable of putting to use all of the information content (in a Shannon entropy sense) given by the diagnostic. Some (maybe most) of the information is thrown out in this process, and these diagnostic signals may contain information about plasma behavior that is currently unknown or tedious to deduce in a traditional context. This information may be useful for, say, real-time control or instability suppression that would otherwise go unnoticed or unused in traditional diagnostic processing approaches. 

Autonomous experiment exploration

Armed with more information about plasma state (albeit likely in an incomprehensible representation), our (referring to the union of machines and humans) ability to exploit this information may be greater. Autonomous manipulation of plasma actuators by an AI agent may be the best way to find new plasma behavior and solutions to problems in plasma control. Human intuition and processing, although powerful, takes a very long time to perform and iterate on. Removing humans from this analysis loop may improve and hasten optimization of plasma (or reactor) state. 

Some sort of novelty search over plasma parameters space could also be performed by attempting to predict where the learned model has a high cross-entropy (or “surprise”) and verifying the prediction. However, I do not have a good intuition on how such an autonomous novelty search is built and how difficult they actually are to execute. 

It would be interesting to see if an active control AI benefitted from having some human-physics-based representation of the plasma state. It may also be a good idea to try to find some way to hardcode previously learned human physics representation into the model—the human representation may actually be the “correct” way to think about these problems. 

Speculation / idea: making simulations more useful

Machine learning may provide a pathway to a combining simulation and experiment. It may be possible to construct whole-device models using some sort of generative-adversarial approach where the simulations give an “outline” or rough estimate of plasma behavior, and finer structure is filled in using diagnostics. In a sense, the plasma parameters at certain positions get pegged to particular values (or a range of values) by diagnostics and the models massage the simulation results accordingly. This approach could lead to a better understanding of a plasma device. However, combining multiple diagnostics and simulations together into some sort of representation that’s “understandable” for neural networks (or another AI technology) is probably non-trivial. Some work may have been done before on bridging simulation and experiment (presented at DPP 2018) but I do not know if anything has come of it yet. 

Machine learning techniques are still young and dumb At the moment, machine learning techniques are still being developed and their properties and behaviors are not fully understood, if at all. This deficiency in understanding does no favors for scientific interpretability. What’s the point in learning physics in a completely opaque representation if it does not generalize well and extending knowledge beyond the model is nigh impossible? These methods could completely fail.

The best we’ve seen in reinforcement learning is RL agents playing Dota 2, and that took much more computing power than what’s available to a university project. Whether or not autonomous experiment exploration and instability suppression is an easier problem is still undetermined. Model- and ML-based active control is also a very young field. I have no idea how well these methods work and how easily they’ll be applied to plasma problems.

Biases

My bias towards linear devices 

I work on mirror machines and have read a lot about their advantages and disadvantages, but I am still quite young and didn’t live through the era when the disappointing performance of these devices might have been acutely felt. For this reason, I may have a distinct lack of perspective that compels me to favor mirror machines and linear devices over tokamaks. I may also be underestimating the amount of work that it has taken us to get to our current understanding of tokamaks. Because they have been better studied and are widely discussed, the drawbacks of tokamaks are more readily apparent to newcomers to the field, such as myself. 

My biased optimism of machine learning methods and desire to do cool shit

I have studied, read, and played with machine learning a great deal. I think I am fairly aware of their capabilities and drawbacks, but my desire for working on “cool” or “sexy” things may make me want to work on projects using ML techniques that may be entirely bad ideas. I don’t quite have an intuition on how hard these projects actually are yet. I may also be overestimating the potential and rapidity at which techniques, like reinforcement learning, advance. 

My bias towards wishful thinking

I’m concerned about wishful thinking. I think it’s very easy for me to get into a state where I’m overly optimistic about the future and potential outcomes because I really want it to be true. After all, I grew up with science fiction and I am attempting to make that into a reality. These dreams may bias me into choosing projects that are not achievable and more nutty than others. These reasons are why I am sending this document to you and many others; I’m not quite sure how closely my thinking aligns with reality. 

Project ideas (rough)

My goal is to do something maximally useful for the fusion community.

Autonomous experiment exploration

Goals of the project

  • Identify simple plasma phenomena to rediscover
  • Attempt to discover with autonomous ML, manually controlled ML, RL, or another data-driven control scheme
  • This seems super hard—don’t know where to start

Simple phenomena

  • Start with simple / understood thing

High rep rate

  • More data = better
  • 1 Hz = 605k experiments in a week

Inter-shot (and possibly intra-shot) control of instabilities, flows, or transport. But preferably instabilities

This is super important because fusion devices are fundamentally limited by instabilities.

  • Identify instability or phenomenon that’s easy to control and try to train an ML model to solve
    • Shear flow in LAPD using biasing
    • Interchange (may be hard because of small length scales? (what is the k of interchange modes anyways?))
    • Kink modes (flow-stabilized z-pinch is a thing)

System overview — how to get from probe data to ML system to feedback

  • Two options: derive “physical” quantities from probe data, or use raw voltages / currents / bits
  • Shaft-mounted diagnostics may be challenging to use because each shot is different and you need to move it around to collect lots of data. Perhaps using an array of these probes could work. Or just collect data at one position
  • Need some way of quantifying the instability so you know what to minimize
  • One of the ways of determining interesting spaces is to know where you are extrapolating, and testing those extrapolations with the learned models. This could be a thesis itself.

Model components?

  • ML model where behavior of the plasma is predicted given actuator and machine state values. Model needs to be invertible (maybe an autoencoder of some sort) so that solving the inverse problem is easier
  • Policy to decide which direction to pursue—maybe by sampling the learned model
  • Choosing next actuator values (maybe done by hand, maybe some SGD analog, maybe RL)
  • Metalearner for easy transfer of knowledge to slightly different domains

Model overview

  • Feed time series data into a WaveNet-like or RNN-like architecture.
  • Part of the time series data analysis should be physics-based to determine the existence of the instability
  • Time series data should include actuators (either time-varying or static)
  • Train with varying degrees of dropout on all data streams so that resilience to equipment failure is built into the model automatically?
  • All of the data are reduced into a simpler, lower-dimensional, latent representation which is fed into the learning models (probably NNs or CNNs of some sort)
  • Diagnostic data is correlated with actuator input
  • Some sort of meta-gradient descent is used to determine a way to suppress the instability? Derivatives are found by slightly adjusting actuators and determining the slope?

Diagnostics and device specifications

  • Need globally diagnosed plasma so that improvements can be made at each shot

What fusion should look like in 16 years (2035)

  • Experiments performed autonomously
    • Start with existing theory or model (can be done loosely in an NN I suppose)
    • Might be able to ignore plasma theory entirely (probably not a good idea)
    • Need some way to autonomously explore parameter space
    • Need some way of knowing what is a good / interesting regime to go in (suffers from same exploration / exploitation problems that plagues like every optimization routine)
    • Need to learn the response of the plasma to actuation
    • Metalearning is probably the key to this. Designing models for specific conditions and then interpolating across them. Not sure though. Reinforcement learning is probably not the way to go.
    • We’ll be training on raw signals instead of on physical quantities derived from them
  • Instability suppression is performed autonomously
  • Optimized towards energy confinement maximization in a tandem mirror. So you will need at least one physical metric.
  • Machines need to be built so that maximal data can be captured in just one shot instead of like 1000

Thesis ideas

  • Predicting plasma state (also integrating existing physics knowledge)
    • Perhaps includes constructing a fast whole device model
    • Meta-learning may be the key for integrating physics knowledge and interpretable learning
  • Autonomous experiment selection and execution
    • Ideal for fusion parameter space exploration
  • Design and construction of high-rep-rate plasma device as a testbed for ML / AI algorithms
  • If I am using the LAPD for data collection, we need the following to maximize the success of my project:
    • Global diagnostics digitized on every shot (magnetics would be easiest, fast camera would be nice)
    • Standardized channel multipliers in the HDF5 file to minimize the need of hunting down people for information
    • Map LAPD data to ITER Integrated Modeling and Analysis Suite (IMAS)
  • Need macroscopic, interesting phenomena to model. Might include need to crank up that ICRH antenna to get interesting behavior
    • Just predicting plasma state in regular LAPD discharges seems kind of boring. Could try to predict fluctuations in probes, but that seems very difficult to do when the plasma is very under-diagnosed.
  • No tokamaks please
    • Hard to do experiments (takes a lot of time to get shots I / the AI would want)
    • Very low rep rate (10’s of minutes). TAE’s C-2W has a rep rate of ~8 minutes, limited by inertial cooling of internal coil.
    • It’s better to start with a much simpler system to see if the techniques even work in the first place. Small steps are better than large ones.