Photo of Dr. Carla Shatz, Professor at Stanford and Director of Bio-X, standing in front of an indistinct background and smiling. She has her short dark hair tied up and is wearing glasses.

Photo by Thor Nielsen/NTNU (Norges Teknisk-Naturvitenskapelige Universitet): Dr. Carla Shatz.

Nature Neuroscience - June 2, 2023 - Shari Wiseman

As Nature Neuroscience celebrates its 25th anniversary, we are having conversations with both established leaders in the field and those earlier in their careers to discuss how the field has evolved and where it is heading. This month we are talking to Carla Shatz, who is the Sapp Family Provostial Professor, Catherine Holman Johnson Director of Stanford Bio-X, and Professor of Biology and Neurobiology at Stanford University. Her work has illuminated mechanisms of visual system development and plasticity and has focused more recently on synaptic pruning mechanisms.

How did you get interested in science? And how did you get interested specifically in neuroscience, or what we now call neuroscience?

I was an undergrad at Harvard (at that time the women’s college was called Radcliffe), and I was majoring in Chemistry. I really loved science but I also really loved art and visual design. I think that’s because my dad was an engineer and my mom was a painter. I was lucky because at the time, it wasn’t very common for women to become scientists (I recommend the marvelous novel Lessons in Chemistry1, which does a fantastic job of capturing what it was like for women in science then), but my parents both told me, “Don’t worry about what anybody else thinks of you, just follow your heart.” I think it was a good idea and also a bad idea because there was only one other woman in my class who majored in Chemistry, so it was a pretty lonely period.

I was looking for this intersection of art and science throughout my undergraduate career, and luckily I found it. In my senior year, I went to my chemistry professor, and he listened to me and said, “Well, you know what? I know these two young professors at Harvard Medical School and they’re working on the visual system. Why don’t you go and see if they would take you for your senior thesis?” So, guess what? It was David Hubel and Torsten Wiesel.

Not too shabby.

Apparently I was also the first undergrad to approach them, so they were intrigued. So they took me for that year and the rest is history because it was so exciting. I couldn’t believe what I was seeing. They were trying to figure out the fundamental rules of information processing in the central visual system. So that’s the story from me being a kid and liking both science and art all the way to coming back to grad school with them.

The other thing that I think is important to remember is that at the time that I was a nerdy high school student, it was the Cold War and the Space Race in the US. The satellite Sputnik was launched by the Russians first and our country decided to put a huge amount of resources into science education and public schools. I think about that a lot now, when I think about the state of public schools in our country and the lack of investment. Hubel and Wiesel’s generation was influenced by World War II, and people like Hodgkin and Huxley were working during the war in signal processing and radar, and they brought their electrical engineering skills into their subsequent research. That’s why the first in vivo functional studies in the nervous system were using electrophysiology. During the course of my career, starting with pretty much only being able to do electrophysiology on a living organism and going all the way to now, it’s been an extraordinary and never-ending adventure, like the best mystery in the world, because you never know what new thing someone is going to invent to allow for the next breakthrough. That said, I do have a concern about our modern emphasis on techniques. I feel like there’s a real opportunity to go back now and ask some pretty profound questions about nervous system development, organization, function, and disease rather than the huge emphasis on technique building.

Research nowadays tends to be less hypothesis-driven and more kind of ‘-omic’, looking at everything all at once rather than focusing on a specific circuit or a specific signaling pathway. I’m interested in how, over the course of your career, you’ve decided how and when to incorporate new technologies or approaches. You don’t want to chase the hot new thing, but you also don’t want to miss out on the opportunity to make a discovery.

Right now, everything is BIG. My lab has always been organized around The Big Q, the Big Question, rather than the big technique. I am a great fan of people who develop new methods, but my own approach has really been to follow the question.

From the very moment that I started in Hubel and Wiesel’s lab, I was completely blown away by the elegant organization of the nervous system, and particularly the visual system. They were in the process of discovering the ocular dominance columns and the orientation columns and thinking about how they could reveal them not only with electrodes but visually with 2-deoxyglucose and other techniques. They were also studying in detail the developmental critical period in the visual system and the notion that visual experience could influence the final outcome of development of a circuit. And those were very profound questions. So I got really interested in, “How does this amazing machine develop?” and so that has been my big question. And I’ve tried to follow that and use every technique available at the time to answer the question.

I’ll give you an example. Discovering the retinal waves2 really took advantage of two things. The first was the perfection of Ca2+ imaging using the confocal microscope, and it turned out that Steven Smith was right down the hall from my lab, and Rachel Wong, who was a postdoc in my lab at the time, went to talk with him about using Ca2+ imaging to look at activity in the retina. And then Marcus Meister was a postdoc in Dennis Baylor’s lab, and Rachel and I went to them and we said, “Hey, you’ve been doing these salamander retinas. Can we try our little developing ferret retina on your multi-electrode array?” And that was amazing. And then Marla Feller came with her optical physics background and developed these extraordinary microscopes, and that’s when we really saw the waves3. People had been making computational models of how the eye-specific layers might form in the lateral geniculate nucleus of the thalamus. I had been thinking about it in terms of, “Cells that fire together, wire together,” a term I coined. There was a big argument about whether the layers are hard wired, or is neural activity or experience needed to form the layers. The problem was, how do you actually record from more than one cell at a time? Nowadays, no problem. But at the time, because of the advent of multi-electrode arrays and Ca2+ imaging — you can’t imagine how amazing it was to see with your own eyes.

With the Ca2+ waves, it’s so incredible that you had the question of whether the refinement is hard-wired or activity-dependent, and the answer was, “It’s both.” It’s spontaneous waves, so it’s activity, but it’s not related to sensory input. That must have been such an interesting surprise.

It was a great surprise but it also was very controversial. People said the waves were an artifact, or spreading depression, which had been studied in the cortex, or that it had to all be totally hardwired because it was happening in utero. We did a lot of experiments to convince people, but I can tell you it was pretty hard to get the first paper published. We had to do a lot of homework, which I think is okay when you make an unexpected discovery. Now, people realize that spontaneous activity and highly correlated patterns of activity early in development tune up circuits to be ready for their later function.

Coming out of these very prominent labs, was it hard for you when you started your own lab to find your place and get established as an independent investigator?

Well, let me put it this way: it was hard, but it wasn’t hard. Let me explain. First of all, I was so driven by this question that I was not concerned about whether I was going to be competing with anyone, including my postdoc advisor, Pasko Rakic. Nowadays, as my postdocs leave, I’m so excited to break the bottle of champagne over their ship as it sails away, and we have these conversations about who’s going to do what, and I try to stay away from their chosen area, at least for a few years. But in the old days you never had those conversations.

I wanted to take a deep dive into the cellular and molecular mechanisms of activity-dependent development. What led me into the discoveries of retinal waves was really to try to set up in my own lab a system for studying the development of the retinogeniculate pathway. I thought studying the eye-to-brain connection would be practical because the access to the developing retinas is immediate — you don’t have to go into the brain. And, from a developmental biologist viewpoint, the formation of the eye-specific layers is kind of a dream because it’s a beautiful pattern that is recognizable. If you do a perturbation experiment, you can quickly see whether you’ve changed the pattern and then you can study it.

At the time that I started my lab, Pasko had been doing all these beautiful experiments in non-human primates and I knew that there’s no way anyone except him could continue to do that kind of thing, and that he was really interested in cortical development. So, I found a niche, partly because I had a question that I was interested in, but also partly because the territory wasn’t highly populated. Even now, in the area of activity-dependent development, there are so many opportunities where there are uncharted waters, so it kind of pains me when people all go down the same path. It’s all meaningful, so don’t get me wrong, but they’re not necessarily going to find some crazy new thing that’s unexpected. There are still so many opportunities, but I think you actually have to know the literature to see where there are major holes. For example — here’s a good one — we know something about axon pathfinding and target selection, but we still really don’t know what the target-derived molecules are that guide axons to the lateral geniculate nucleus and not the medial geniculate nucleus, say, or even the appropriate cortical area.

I had always really wanted to push things to where we could study the underlying cellular mechanisms of synaptic plasticity, and then also try to discover molecular mechanisms for synapse elimination and remodeling. If you look at the arc of my career, I think it’s kind of unexpected that I am now studying Alzheimer’s disease4. Whoever thought that by studying developmental mechanisms of activity-dependent synapse remodeling you might actually find mechanisms that are relevant to synapse loss in aging and Alzheimer’s? They’re fundamental developmental mechanisms that get kind of put into hyperdrive — at least that’s my viewpoint.

You mentioned some open questions related to axon guidance. Are there other areas that you think have been dropped or left behind that should be taken up again?

One area that’s evolving is the question of how neurons decide which connections to keep and which to eliminate. We all now agree that neural activity is involved, but we haven’t resolved this question about synaptic tagging and local decisions that synapses make, which is relevant to both development and memory formation.

Just hearing the phrase ‘synaptic tagging’ gave me a little jolt. It was such a hot idea for a while, and you rarely hear it discussed anymore.

Right. And yet it’s completely relevant. Or, for example, there’s a lot of interest in glia and synaptic pruning and engulfment. But less studied is the notion that glia are not just randomly chopping off synapses. There is information there about which synapses should be removed, and the glia have to be part of that mechanism. It’s not just activity-dependent, it’s local activity-dependent, and that’s a concept that involves having synaptic tags. And what is also important with all of these diffusible molecules is, where are the receptors? This is why we’ve been following PirB, which is a receptor that mediates pruning.

The other thing that I think is so amazing right now is the ability to begin to look at the human condition, so you can really ask whether all the stuff you study in mice is even relevant. I think it’s exciting both in the context of looking at high-quality autopsy material and being able to actually look at human neurons or neural organoids in a dish.

You’ve held a lot of leadership positions in your career. You were Chair of Neurobiology at Harvard Medical School, you’re Director of the Bio-X initiative at Stanford, and you were President of the Society for Neuroscience, in addition to leading your own lab. What has that meant to you? What do you see as your responsibility or your mission?

First of all, I just feel gratitude. Even though it has been a struggle as a woman, I feel grateful for being given the opportunity to pursue this career. I am incredibly privileged to have been able to have been at all these great places. As an aside, it’s pretty funny when you’re a graduate student in the same department where you later come back to be the Chair. Just a bit of advice to the senior people is to remember that any one of your students could come back and be your boss someday.

The main thing is, to be really clear, there was no one who ‘looked like me’ when I started in science. That has always bothered me, and so part of my mission has really been to show up and represent women scientists, and I’m very proud of that. At Harvard, when I was Chair, not only did I hire some amazing women faculty, but there were so few women faculty at the time that it actually changed the total percentage of women in the basic science departments at the Medical School. When I came to Stanford to run Bio-X, I really loved it because it was an opportunity to embrace and support very high-risk, potentially high-reward interdisciplinary research. And this is one of my big concerns right now, that we’re not supporting enough really early stage fundamental research. I really worry about that because big surprises come sometimes from the most unexpected places.

I’ve tried hard to support women’s careers in science, and it’s been quite an honor. I’ve had a wonderful lab of both men and women over the years, but it’s always been at least 50/50, if not more women than men. My scientific offspring are probably the most important contribution I can make in my entire career. Looking now at where we are versus where we were when I started, it’s just incredibly exciting and heartwarming to see that the entering graduate class coming into a Neuroscience PhD program or med school is 50/50, if not slightly more women now. So part of the reason to take some of these leadership positions is to just have people see that women can do these things.

Some people might be annoyed by the ‘we need a woman’ thing. But, when I was hired at Stanford for my first faculty job as an Assistant Professor — I didn’t find this out until later when I got tenure — the Medical School had offered a free extra faculty position to any department that would hire a woman, and only one other department took up the offer (the other woman, Helen Blau, and I are both in the National Academy of Sciences now). Also, I was the first woman to get a PhD from the Neurobiology Department at Harvard. Years later, David Hubel told me that they had a big discussion about whether or not they should accept me into the PhD program because the feeling was that I was probably just going to go get married and have kids and go away, so why should they ‘waste the training’? So, thank goodness, things have changed! We have a long way to go still to increase diversity, don’t get me wrong. People want all of these things to change overnight, but when I look at women in science, if you look at how long it’s taken, it’s been a persistent pressure the whole time.

I should end by saying that it’s never finished. I think a good example of that is the recent revocation of women’s rights to reproductive choice in many US states. You learn that you cannot give up, even if you think you’re done with something. We always have to be vigilant, and we always have to work toward an even better future. Not only now for women, but also for other groups. It’s now the next generation’s turn, and I hope those in my generation have helped to build the road.

Nature Neuroscience (2023)
doi: 10.1038/s41593-023-01371-y

Originally published in Nature Neuroscience