OHBM 2020 Keynote Interview Series: Q&A with Michael Fox

By Nils Muhlert

Michael Fox

Professor Michael Fox is a neurologist at Harvard Medical School and director of the Lab for Brain Network Imaging and Modulation. His research into brain network imaging to define targets for brain stimulation holds considerable promise for new and improved treatments for a wide range of neurological and neuropsychiatric conditions. Here we found out how his academic career started through a chance meeting with Mark Raichle, about his plans for clinical translation of network neuroimaging, and his advice for early career researchers:

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Nils Muhlert (NM): Thanks for meeting with us. We'll start by finding out about your background. How did you become interested in neuroimaging?

Michael Fox (MF): Good question. I didn't start off life as a neuroimager. I was an electrical engineer as an undergrad and then went to Washington in St. Louis for my MD and PhD combined. I wanted to do something at the intersection of engineering and medicine. My interest in neuroimaging came when I was walking through the neuroimaging facility at Washington University in St. Louis, on the way to a meeting. I saw a poster hanging there in the hall by Mark Raichle looking at brain imaging and the default mode network. I stopped, and I read the poster and thought, wow, that's fascinating. I had no idea who Mark Raichle was, but I subsequently knocked on his door and said, “Hey, I'm Mike - I just read a poster out here that I think is really interesting.” And that's how I got interested in neuroimaging.

NM: And how have you found the challenges of balancing your clinical work with your academic work?

MF: It's a challenge! There's always time constraints. On the side of getting out papers and getting grants, your clinician-scientists have to compete with full-time scientists. And with the challenge of taking care of patients, our clinical care has to be up to the same standard as full-time clinicians. It's like you're doing two jobs at once, and you have to be really good at both of them.

But with that challenge comes enormous opportunity. I wouldn't be doing both clinical and research if I didn't feel that it was valuable, and that one inherently informed the other. I don't feel like I'd know what the relevant research questions are to ask or to go after if I'm not seeing patients. Similarly, I won't know how to take care of my patients as best as I could, if I am not up to date on what the research is telling us about how to think about the brain.

NM: A lot of your work uses network neuroscience to understand how lesions in different locations in the brain can lead to similar symptoms. Can you tell us about this lesion-network mapping, how it works and how it can translate into the clinic?

MF: You asked me earlier: "how does research inform clinical care and clinical care inform research?". Well this entire field came from a patient. Aaron Boes, who was a fellow of mine at the time, saw a patient that walked into the clinic with acute onset visual hallucinations. Radiology acquired a brain scan on that patient and they found a focal lesion in the medial thalamus. Aaron Boes was fascinated by this patient. Why is it that a lesion in this particular location could result in this very impressive rapid onset severe visual hallucinations?

Aaron did what any good neurologists would do: he went through the literature and found other similar cases of patients with brain lesions that caused acute onset visual hallucinations. He mapped out where all of these lesion locations were, and then was left scratching his head.

All these different cases that cause symptoms very similar to what his patient had, were all in different locations across the brain. That's when he had his critical insight. When I'm trying to understand this patient's symptoms and I map out all the locations of brain damage, they don't line up. They don't intersect a single brain region.

Aaron literally came and knocked on my door and said, "Mike, I hear you do some kind of brain connectivity thing; could that brain connectivity stuff could help us understand how all these lesions in different locations are causing the same symptom."

Aaron's insight, which was in retrospect really brilliant, was that you can take a map of brain connectivity, overlay the lesions on a brain network and test the hypothesis that lesions causing the same symptom map to a single connected brain network rather than a single brain region. He was right for visual hallucinations. And subsequently, I think he's been right for every other neurological or psychiatric symptom that we've tried to investigate.

It's not really a new idea. Neurologists have known for a long time that symptoms probably mapped to brain networks or brain circuits. But before we had a wiring diagram, it was very hard to test that hypothesis or figure out what the network or circuit was in a data driven manner.

NM: How does it work in practice?

MF: In practice, you derive the network for each lesion location. So when you have a lesion that causes a certain symptom, you map it onto a brain atlas. You then turn to a connectome database and say, "Okay, I know where the lesion location is, but what I think is relevant for symptoms is everything that lesion location is connected to." So you turn the lesion into a lesion network, and you do that for every single lesion that you're interested in. Now, every lesion is going to be connected to hundreds of different brain areas, right? But if you take 40 lesions that all cause the same symptom, each one of those 40 lesions is a very different brain network or different set of connections. But the one thing that those 40 lesions share should be the connections that are relevant to the one symptom. And that's how you're able to then pull out the circuit that's relevant for that symptom shared by those 40 lesions.

NM: That's great. So this is a great example of how open science, through the human connectome project, has the potential to influence clinical practice...

MF: Very, very much so! I often feel a lot of gratitude for the field of neuroimaging as a whole  and all the people out there that work so hard to build these connectome databases. If we didn't have things like Randy Buckner's genomics superstruct project, which is the connectome that I use for most of my work, if we didn't have the Wash U connectome, if we didn't have the MGH DTI connectome, then we wouldn't have the wiring diagram that allows me to do all the work that I do. So I'm very grateful to neuroimaging and grateful to these large scale projects that gave us these wiring diagrams. I'm just a user of this amazing resource that other people built.

NM: That's great to hear. Right now it's tricky to carry out clinical research projects so I imagine these large open databases are being well used. One topic that people have debated, particularly over the last couple of years, is clinical applications of fMRI.  Your work seems to allow that - using functional brain networks to identify the targets for deep brain stimulation. How did you find the process of convincing people of the suitability of that approach?

MF: You're getting really to the heart of it. My PhD was focused on neuroimaging, and so when I moved into the clinic, and in my residency focused on trying to help people with brain problems, there was a disconnect. The field of functional neuroimaging does not have a lot of success stories. The idea was: "Hey, if we can see the brain at work, and identify areas that light up, if we can see the brain's connectivity, if we can look at the anatomical connectivity based on things like diffusion mapping, that all this will lead into better clinical care, better diagnosis, better outcomes, better treatments.” We don't have a lot of successes to hang our hat on. Even preoperative mapping with functional MRI is only used by a handful of centers. There's still debate as to how valuable it actually is. And that's probably our number one success story of clinical translation of functional neuroimaging.

So I've spent a lot of time thinking through why is that? One reason might be that we're on the right path but we need higher cohort sizes, better scanners, the next greatest imaging technique to show us something in the brain that we couldn't see before.

The other possibility is that we're approaching how we use neuroimaging to improve clinical care in the wrong way. I don't know the answer to it, but there's a couple of shifts that I've made in how I use neuroimaging and how I think about it. One big shift has been away from correlation imaging to causal mapping of human brain function. What I mean by this is that if you want to understand where a symptom lives in the human brain, neuroimagers have typically approached that by taking a bunch of patients with that symptom, and identified neuroimaging correlates of that symptom, which might be atrophy, PET metabolic patterns, resting state connectivity changes, and so on. But the problem is that in the end, that's just a correlate, not a therapeutic target. It doesn't tell you whether that neuroimaging correlate is causing the problem, compensating for the problem, or just a risk factor for the problem. We've started focusing on brain lesions and brain stimulation sites as a way to get at this causality. The idea is that the causal mapping of symptoms and brain function might be a more direct path to a treatment target.

The other big shift that I've made is a move away from focusing on single subject neuroimaging data to group neuroimaging data like the connectome. It's almost like I'm going in the opposite direction of where a lot of brilliant people are going: they're focusing on the individual and getting massive amounts of data on each single subject. That research is very valuable and might get us where we need to go with the clinical utility of single subject imaging data. In the meantime, as they improve the methods and technologies for single subject imaging, what I found is that the group connectome is already ready to be applied clinically. It's robust and reproducible and the wiring diagram is the wiring diagram of the average human brain.

NM: So we've very high hopes for your work targeting sites for stimulation to reduce symptoms in patients.

MF: Well, I don't want to overstate the success of my approach either. What we have right now is a lot of retrospective observations. So when we administer transcranial magnetic stimulation, for example, to try and reduce people's depression, what we see reproducibly is that people that are stimulated at a certain brain circuit or a certain site that's connected to a certain circuit, those are the people that are getting better. That is a reproducible, retrospective observation to explain why some people are getting better and some people are not. What we haven't done is taken the next step, where we change our clinical practice and directly target that circuit to improve clinical outcomes. We're just now reaching that precipice, the point where we're convinced that the retrospective observation is real and reproducible. But now we've got to actually prospectively apply it and find out if we can improve clinical outcomes, but we haven't done that yet.

NM: So what would you say are the most exciting things that your lab is working on now?

MF: I'd say, twofold. One is I'm very, very excited that we're reaching the point where we can take some of these retrospective observations and actually prospectively test them clinically. Now, those are bigger grants and take a lot more money. But I believe those resources are going to be coming. So I'm very excited to find out whether we can prospectively confirm our results and make treatment better.

The other is focusing on symptoms that are in huge need of better treatment. We recently submitted a paper, for example, on lesions that get rid of addiction (for a similar paper see here [NM]) and what brain circuit do those lesions map to? Does that identify a therapeutic target for addiction that can help constrain ongoing trials trying to make addiction treatment better?

In the field of depression, we've worked on brain lesions associated with depression, TMS sites that are associated with depression relief, and then some deep brain stimulation data that either can relieve depression or cause depression. What happens when you link up all three sources of causal information? Does it all converge on a single circuit target for depression across all these different modalities? 

On the science side, we're even working on lesions that manipulate measures of spirituality or religiosity. Is there a human brain circuit that we can link to spirituality in a causal way? And is that a therapeutic target?

We're having a lot of fun these days, looking at very interesting questions both from the scientific side of things and social side of things, but also going towards the greatest therapeutic need. And then going towards clinical validation of all these observations that we're coming up with.

NM: Finally, what is your advice for early career researchers and those who are interested in network neuroscience? What would you say is a good training pathway for them?

MF: One piece of advice is follow your passion. If you're passionate about a particular brain problem or symptom or imaging technique, or brain circuit, follow that passion because your work is going to be better if you're following something that you're passionate about, not just what your advisor is passionate about.

Two, look at where the herd is going, and then intentionally go in a different direction. If everybody believes that the next big advancement is this imaging technique or application, then go the direction they're not going. Because there's plenty of people that are already doing what the herd is doing. That's why the herd is going there. It's an obvious need and a lot of smart people will fill that need. Go the opposite direction, find a way that people are not thinking about it. And that's where you feel like you add value to science, above and beyond what the community can generate. Think about it differently.

The last piece of advice is one I always tell my students. In my particular lab, we're focused on clinical translation and clinical application. So whenever my students come to me with brilliant ideas (and they come to me with brilliant ideas), I try and play it out. I say "Okay, let's say you're right, let's say that the experiment works out or that you're able to map it. Where does that go? What do we do with that information?" Oftentimes, you realize when you play that out is that the experiment, although it might be interesting, has no pathway towards clinical translation. There's no way that you can turn that information into a better treatment or a therapeutic target. Now, not everybody's interested in clinical translation, identifying therapeutic targets, but for my lab, thinking ahead three steps, we want to know 'Where does your research go? What do you do with that result? And how does that result translate into something important and meaningful, in my case for taking care of patients?' Again, it's a different way of approaching things then maybe in other neuroimaging labs.

NM: That's great advice. Professor Fox, thank you very much for your time today. We really look forward to your talk.

MF:  Thank you so much for your interest.