Basic Medical Research Award
Part 1: Early Education and Medical School
Dr. MacKinnon describes his upbringing in suburban Boston, his early interest in science and his earliest years in Dr. Miller's lab at Brandeis. He also discusses his decision to go to medical school and its impact.
Dr. Miller: So why don't you just tell a little bit about your personal background and sort of the trajectory by which you arrived at the place you are at now.
Dr. MacKinnon: An unlikely trajectory. I was born in Burlington, Massachusetts. I'm a Massachusetts boy. The middle of a family of seven children and grew up in Burlington, Massachusetts. Went to the public school there, and my parents moved to Cohasset when I was in high school, in ninth grade, (they) moved to the South Shore of Boston. So I'm a Boston suburbanite, all my life. And related to science, you know my parents are not scientists, and I, in fact, didn't know any scientists when I was young, but I always loved science. They were my favorite courses in school. And I guess you could say that it became clear that something wasn't quite right when in junior high I wanted to go to summer school because it was a science enrichment course, and I got to have a microscope there, and I could take the microscope home for the summer. I used to like to go around and look at pond water and blades of grass, and I was thoroughly amused by these things.
I think I was a very typical average little kid in most respects. But when I really did get turned on to science is when I went to college, to Brandeis University. And there I went from public schools in suburban Boston to Brandeis University, and that was a real eye opening experience for me. There were a lot of my peers there, my classmates, who were from different backgrounds and I just... It was a real good time. It was from 1974 to 1978. Brandeis was a wonderful place to be then. I had a lot of fun, and it was a real intellectual experience, and my exposure to classroom science was very good there. But in particular, Chris, as you well know, I came to your lab and worked on calcium pumping in the sarcoplasmic reticulum. I was the third member of your lab, you being the first, Gribet your dog the second, and I was the next. When you had just set it up. And it was a special time. I have a lot of emotions attached to that, actually, in the little lab.
Dr. Miller: We both do.
Dr. MacKinnon: It was a very bright lab, big windows. The sun would pour in, and it was just a happy place to be. It was a wonderful time. I ended up going to medical school.
Dr. Miller: Against my strong advice, if you remember.
Dr. MacKinnon: I remember very well. In fact, I think the real reason I went to medical school was not because I was ever pushed to do that, but I was naive enough to think that the practice of medicine was close to the carrying out of scientific experiments, and I learned that it's quite different. You use a different part of your brain in solving problems in medicine than in solving problems in a more analytical kind of way. Here's the puzzle, can you solve it? That's what I loved about science and do love about science. But I think I went to medical school because that's what everybody seemed to be doing, and I did think it was a lot like laboratory science. It took me a long time to figure out that it's very different. It's very special in its own way. I don't have any regrets, but I know that when I came back to you eight years later and said, "You know I've been thinking about what you said, and that is that I should get a Ph.D." You know it's a funny story, and it's absolutely true. I came back eight years later and said, "You know, you were right." And, fortunately, because then I could get a postdoc.
Dr. Miller: Yeah, you didn't realize that. You thought you had to go back to graduate school. And I said, "You dummy, you don't have to get a doctorate, you already have a doctorate."
Dr. MacKinnon: I had completed medical school in four years and three years of residency with the plans to practice medicine. And although I felt like I was getting old at the time, close to 30 years old, I just thought about, "Gee, when I'm much older than this, I'll look back and say, gee, that was actually young. So just go for it." So I thought I should go to graduate school and get a Ph.D., and you advised me that I wouldn't need to do that. So that's when I came to do the postdoc at Brandeis with you, in the same lab, and started working on potassium channels.
Dr. Miller: I think your medical education actually gave you a tremendous kind of insight that allowed you to do some of this work in a way that was very different than if you had gone through the sort of way that I had suggested.
Dr. MacKinnon: Well, I think it did in the following way: One of the things that I did in medical school... Well what it did, it taught me to teach myself very well. A little background to that is that while I was going through medical training, I felt I had a need to exercise my mind in a certain way, and I applied mathematics. It became a hobby of mine, and I kept studying those things, and that was good for me. And then when I came to your lab, I had a real sense that I was way behind. And so I read and read and studied and, you know, I'm very diligent about these things. I have stacks of notebooks where I derived things, and I just wanted to make sure I understood things completely. In a way, what that did for me is it taught me to be very independent by just going to learn something. And I think if maybe had I gone to get a Ph.D., I would have... I don't know what would have happened, but this way I certainly know I learned to fearlessly pick up books, go get books and learn a subject, and that certainly came in handy as time went on. That sort of approach.
Dr. Miller: Yeah.
Part 2: Roots of Later Work at Harvard
A suggestion by Miller that MacKinnon work on a scorpion toxin yields many wonderful results. When MacKinnon set up his own lab at Harvard, he says, "the most exciting points that stand out in my mind are the experiments showing that potassium channels had to be tetramers."
Dr. Miller: Well, why don't you just say a little bit about when you started your own lab, and then what kind of research you started out doing and how then, what made you make this big essentially almost a mythic heroic change into crystallography. I think you are the only person in the field of ion channels who did this. Who just dropped the standard way of studying ion channels that we've all been doing and just said, "No, I am going to now remake myself." Tell the story a little bit.
Dr. MacKinnon: I'll tell the story, but actually the story begins, in thinking about it right now, a little before the transition from mutagenesis analysis that we were all doing. I think the story begins when I came to your lab. Among the things I read, I read the classics of Hodgkin and Huxley. I read the work of Bertil Hille and Clay Armstrong, the sort of electrophysiologist view of ion channel proteins. This field, its background is very different than the rest of biochemistry. For example, the people who taught us how enzymes work, they had their background in protein biochemistry. So mechanistic enzymologists knew all about proteins, whereas, for historical reasons, the study of ion channels compared to enzymes had a very different background. People who studied ion channels were people who knew about resistors and capacitors and amplifiers—very different kinds of people—and less about proteins. So the techniques were completely different. The study of ion channels for so many years was almost like a parallel universe.
Dr. Miller: Different language, different...
Dr. MacKinnon: A totally different language, you know, and when people from the protein world start hearing about capacitance, I think that you know that is something that sounds strange. And likewise when people from the electrophysiology world would start to hear about hydrogen bonding, it would sound equally strange to them. I think the whole field was quite separate. But when I came to your lab, it was very clear to me that in this environment of Brandeis biochemistry, you thought about ion channels the way Jencks and Abeles thought about enzymes. And it's really true. So my introduction to the field is, although I was reading the classic electrophysiology text, I was also being immersed in this way of thinking about ion channels as proteins.
And I remember going over Michaelis-Menten kinetics and at the same time thinking about ion channels in the same way, because your lab was carrying out experiments on sodium channels and potassium channels and analyzing it in very much the same way. You know, trying to decompose free energies of transition states into enthalpy and entropy double daggers, and this was thinking of ion channels as proteins. And so that's where I got my beginning, and so that's where I think for me the story begins, for looking at ion channels like proteins.
You know, a lot of beautiful happenstance occurred because you suggested I work on a project with this scorpion toxin. You had discovered it. You found out it blocked potassium channels, but wanted to know more about the mechanism. And taught me quickly how to use the bilayer and said, study this. And that was beautiful because in a way it was a very, very simple problem. A very concrete question and good for my learning, and to start thinking about binding energy, and having a picture right from the beginning in my mind of what a channel must look like, and the toxin coming on to it. It was just a perfect project to be working on, especially when around the same time, the first potassium channel gene was cloned. The shaker gene.
I mean this is a nice coincidence of events, because then we discovered, of course, that the shaker gene channel was blocked by the scorpion toxins and immediately had a tool to go at and ask where these amino acids go in the three-dimensional structure. So in a sense, it all begins there with thinking about the three-dimensional structure of the potassium channel. And you know, one thing led to the next.
Before I left your lab, we had found the first mutations on the shaker channel that affected the toxin binding and started to have—it was a very exciting result—the first nibbling of information of whether something is on the outside of the membrane or the inside of the membrane. And is it near what we imagine the center of the channel is, where the pore is, or is it far out on the side? So that's where I think it all began. And then in going in 1989 to my own lab at Harvard continuing on the problem. That couple of years was a great chapter, I think, in all of ion channel biophysics for potassium channels. What went on...
Dr. Miller: So much was happening.
Dr. MacKinnon: So much happened. What went on in my lab, in your lab, in Gary Yellen's lab, in Rick Aldrich's lab and others. It was just over a period of a few years where mutagenesis was used, and we discovered a lot of things. It was very exciting. I mean, I would say from my own efforts that the most exciting points that stand out in my mind are the experiments showing that potassium channels had to be tetramers, although that was a result that everybody more or less expected. It was using the binomial statistics and the toxin to show that it absolutely had to be. It was a thrilling set of experiments for me. It gave me this picture that there definitely had to be four subunits symmetrically arranged in a ring, and then the mutagenesis showing the pore loop. Many labs contributed to that, but because of the toxin work that started in your lab and then continued in my lab, we really found this pore loop.
Dr. Miller: That was a totally new idea when you found it. The idea that the pore would be lined by this loop of sequence rather than a transmembrane helix.
Dr. MacKinnon: That's right.
Dr. Miller: Everybody was looking at, where is the transmembrane helix that will line the pore?
Dr. MacKinnon: That's right. We always imagined there would be cylinders going around the central pore and residues on the cylinder, which if you then looked at this linear stretch of amino acids, they would, we assumed, be scattered throughout the protein. But actually that was a very surprising result. And I think an important result for me psychologically—the realization that you had a barrel with the loops reaching in, and what determined selectivity was a linear stretch of the amino acids. Because I always just assumed when you put the polypeptide chain up, put it together, the residues that would be important would be in one region in the structure, but when you unfolded the whole thing, they would be spread out. But in fact, that was not how it was.
Dr. Miller: As you have in enzymes.
Part 3: Burning Bridges
MacKinnon elaborates on his work on potassium channels and speaks candidly about his momentous decision to leave Harvard for The Rockefeller University.
Dr. MacKinnon: As you have in most proteins, right. But in the potassium channel and now we know this is going to be true for calcium and sodium channels and some others. It seems there are determinants in a very small stretch of amino acids. And the reason I said that was important psychologically is because I thought, "Gee, it begs the question, what is special about these amino acids and what are they doing? Why is a linear stretch of amino acids making the selectivity filter of a potassium channel?" We could only take the mutagenesis as far as knowing which amino acids were responsible for selectivity.
But beyond mutagenesis, we couldn't answer the question, why do they do what they do? And that was the real motivation for me then to say, "Okay I have to adopt a new set of techniques." And that's after I was at Harvard for about four or five years that I started thinking this way. And the other thing was, the cloning efforts on potassium channels, cloning efforts throughout the world, showed that potassium channels from every part of life contained the conserved sequence. So then not only did we know that it was a linear stretch of amino acids in a small region that are important, but that nature seemed to be happily settled on one potassium selectivity filter. That begged the question even more. What's it doing and why is it the selectivity filter?
So I thought about different structural techniques and decided that x-ray crystallography would be the technique of choice. So what I did is I, well, I got books. And as I said earlier on in this interview, that was one of the things about my history coming from medicine and then feeling that I had to catch up, I learned to learn on my own very well. That helped when it came to trying to adopt a new technique. And the way I did it was I read a lot of books, and I went and talked to a lot of colleagues who were experts to learn as much as I could. First with purifying proteins and crystallization. So what I did was I started purifying some soluble proteins and trying to crystallize them. One was the scorpion toxin, and I eventually got crystals of that, but they were twinned. And that was around the time we started getting our first crystals of the potassium channel, so I set the toxin aside. But then also, the PDZ domain, that was a good etude, a soluble protein that I could purify and crystallize. Meanwhile, at Harvard a lot of people in the lab thought I was losing my mind because they were, I mean...
Dr. Miller: I think a lot of people in the field thought you were losing your mind, Rod.
Dr. MacKinnon: Well, perhaps I was. Yeah. I had a lab filled with some real talented postdocs and students and they were carrying on the mutagenesis work and analysis with my sort of guidance, but I spent all my time, most of my personal time, learning about chromatography, purification, crystallization and the fundamentals of x-ray crystallography. And then I ended up moving from Harvard to Rockefeller and that was a complicated, I would say a very complicated time and decision in my life. I guess if I think back on it and decide why did I move at the time, I think it was mostly because I really wanted to throw myself off the deep end. I didn't want to be distracted.
Dr. Miller: When you moved you were essentially burning bridges, you felt.
Dr. MacKinnon: Yeah.
Dr. Miller: What exactly were the bridges?
Dr. MacKinnon: The bridges were, I had a lab full of very talented people and the people who were applying to come to my lab wanted to learn—reasonably so—wanted to learn what I was good at.
Dr. Miller: Classical mutagenesis...
Dr. MacKinnon: Classical mutagenesis and electrophysiological analysis of mutated ion channels. And we did learn a lot from that. But I think that's what it was. Nobody wanted to come work with me to do x-ray crystallography. Young scientists in channels don't want to go do crystallography, particularly with somebody who has no record of it. And those in crystallography didn't want to go study membrane proteins by and large, in particular with somebody who had no track record.
So I think the bridges I was burning were those... I was taking away my security blanket of being able to fall back on the techniques that worked for me, and I knew if I just jumped out there and went for this, it was a do or die situation. And when I moved it was just me, one postdoc who had just joined the lab, Declan Doyle, and my wife, Alice. She really felt bad for me and decided that she would work for me, having trained as a chemist. So when we got to Rockefeller it was just the three of us, and that was scary. I was embarrassed to have people visit me, because they gave me a nice lab. I thought people would think, "My God, you know you don't have anybody in your lab. Why do you have this space?"
Dr. Miller: I mean it's true that most, nearly all—I would say all in my knowledge except for you—people who start new directions in their labs, and of course starting new directions is something that every scientist has to keep doing, but the way to do it, the conventional way we all do it is to do it with, just what you said, with a safety valve where most of your effort is still being spent on things you know how to do as you try to learn something you don't know how to do. But you didn't do that. You really just went in to do the things you didn't know how to do. You went through quite a few years without publishing anything, and I guess the question is—I really don't know if you want to talk about this—how did you feel as you stepped away from Harvard into this new lab at Rockefeller, and you really were jumping off the deep end, as you said. How did it feel?
Dr. MacKinnon: I was scared. I was really scared, actually. Do you remember, with this decision I came to you, and I said I really needed to talk. In fact, we got together and we walked down to a little pond in Needham.
Dr. Miller: I remember it very well.
Dr. MacKinnon: And I told you what I wanted to do.
Dr. Miller: The second time I've given you advice that was worthless.
Dr. MacKinnon: Well, you know you thought it was a great idea, but you were more reasonable in thinking why don't you hang on to some of what you do. It will take a long time. But I guess that's just part of my nature, of sort of just going. You know I'm very focused. I think I can only do things if I can focus hard and really brood on a problem and just have no other distractions. And that's what I guess I knew inside, what I had to do to make a go of it. It was frightening.
Part 4: Ion Channels Overview
MacKinnon recounts the amusing "white board" story from his days at Harvard and reflects on the overall state of ion channel research.
Dr. Miller: Just along those lines. That was one of those things ever since I knew you as a young undergraduate and as a postdoc, but I was particularly amazed at it when you started your own lab at Harvard. It seemed to me you had a real, I don't know if talent is the word, but an amazing capacity to not be distracted by all the things that distract us. I think that is something that you've held onto. I remember in your early years at Harvard, I was amazed at how you didn't get distracted—and I think you alienated a lot of people in your department—because of your ability to just focus on your work.
Dr. MacKinnon: Yes, that's right.
Dr. Miller: I remember an incident with a white board.
Dr. MacKinnon: Well, I remember that.
Dr. Miller: I don't know if you want to talk about it. It's a good story.
Dr. MacKinnon: You mean the white board leaning on my wall in the office and the chairman really not finding the appearance of my office appropriate. That's right. The white boards were put there because it was a very good way to organize things and work out little problems, but it looked, I guess it didn't...
Dr. Miller: They weren't mounted on the wall.
Dr. MacKinnon: They weren't mounted on the wall, and I most efficiently used the office space by stacking long white boards that should be hung horizontally, vertically so that I could make the whole wall white boards. And I guess I can understand why the chairman would feel that visitors to the department would wonder, what do they do to young junior faculty at Harvard? They treat them very well, but I was just very focused and very efficient about things. I seldom went to the faculty meetings and the department administrator used to come down. She liked me very much, but was very worried about me and my future, because I wasn't doing everything that I should. You're right, I guess I'm very single minded when trying to solve a problem.
Dr. Miller: Let me ask you about the structure itself, and right now we are still just a little more than one year downstream from what I would call "first light" in ion channels—of actually seeing what the pore of one of these selective ion channel proteins looks like. What would you say are the things that, to your mind, are the most important things we've all, as a field learned, from this? At this early stage in what is now the structural era of ion channels?
Dr. MacKinnon: I think one of the lessons, and that's sort of a methodological lesson, is that the field has done very well in that many of the predictions that were made were very, very good in terms of the general organization of channels, so that the techniques being used by electrophysiologists to study these channel proteins are teaching us a lot. That's on the methodological side, but in terms of the structure and what does it tell us new, I think it answered a few questions and then it raised as many. And I think the kind of question that it answered, and maybe the one that I was most struck by, was how the architecture solved this dielectric barrier problem, actually.
You know the idea that everybody knew for ages that a very basic problem in biology is that because ions, because of their electric charge, they have an electric field around them, and therefore, they are repelled by the low dielectric, oily cell membrane. So nature had to concoct some mechanism for lowering that repulsion called the dielectric barrier. When we saw the first electron density maps, we could see the main helices. But with averaging, the maps were quite good, and we could immediately see that at the center—or half way along the pore—there was a cavity in the middle that was big enough to hold quite a bit of water. And that would be right at the center of the membrane. And then there were four alpha helices pointing their C termini directly at the center of the cavity.
And you know, having studied electrostatics a lot, that aspect of the structure spoke to me. And that was nature's solution to this dielectric barrier problem. That is something I think that the structure simply answered. The use of the pore loop in its organization of amino acids to get the main chain atoms pointed at the selectivity filter was also beautiful. We still need to see this at better resolution to better define the chemistry. But what's very clear is that this is a main chain carbonyl oxygen selectivity filter, and all held together very beautifully by this structure. So these aspects to me, the structure simply answered.
Dr. Miller: What is the question that it answered in the ligation of the ions going through? What was the main mechanistic puzzle about what these channels were doing? That I think your structure really...
Dr. MacKinnon: Yes. Well, very early on the view was, do ions go through the pore hydrated or unhydrated? But I think you know that was very nicely demonstrated through electrophysiology experiments, and some of your own, that the potassium ion is mostly dehydrated. So we knew it was dehydrated, but the question is, how is it coordinated? What atoms of the protein coordinate it? And in fact, there was a hypothesis put forth by me: Could it be, aromatic rings? We could see from mutagenesis a few years ago that the tetraethylammonium ion on the outside was coordinated by a phenylalanine or tyrosine, or a group of four of them in a ring. Because the pore loop amino acids always had some quite conserved aromatic amino acids, we wondered whether metal cations could be coordinated that way as well.
Metal ions could be coordinated by the p orbitals of aromatic rings. And in fact many theoreticians and chemists went and worked on that idea. And still there are some who really like that idea and are quite attracted to it. This structure dispelled it. It doesn't work that way.
In fact, I think some of the questions in my mind that are raised by the structure that are just fascinating are—you know, what it did with the aromatics was actually they are in a cuff around the selectivity filter, pointed away from the selectivity filter, and they form that beautiful plane—and why does nature seem to want aromatics there? And in fact, they are packed in a very unusual way for aromatics. Instead of being herringbone packing with a sort of partial positive edge of a ring against the partial negative face of an adjacent ring, in fact, they're more like edge on edge with funny tilts. But there's a beautiful cuff around there, and I think it has something to do with the compliance or sort of flexibility or lack of flexibility of these rings that ensure that the selectivity filter is quite geometrically constrained to do selectivity. But the fundamental question about is it oxygen carbonyls or aromatics, was certainly answered by the structure, very, very beautifully.
You know fascinating questions that I think about on the structure are, why is this inner wall of the cavity and inner pore, we call it, the part below the selectivity filter that is near the inside, why is that hydrophobic in nature? We proposed that it tends to be inert so that ions won't stick to it, and I think that's right. But I think there's more to it. I actually think it has to do with, the way it structures the water in there, and we won't understand that until we have a higher resolution structure that nicely defines the water—and understand more about water against hydrophobic surfaces. This is speculation, but I find it fascinating.
Another aspect of the structure is that on the selectivity filter... You know the fact that the three ions are in the queue, this was a result anticipated for more than 40 years from the work of Hodgkin and Keynes, and then from the work by you and Jacques Neyton using barium in the calcium activated potassium channel. We knew they'd be in a queue. But then to see them. I think it really said that there must be mutual repulsion in there, as you and Jacques had proposed. To see that and to see how close the ions really are, I think that actually the selectivity filter is going to be an interesting chemical device where the ions not only interact with each other energetically through Coulombs law, but I think they're going to interact energetically through the structure. That is, binding at one position at the end of the selectivity filter perturbs the structure enough to affect the affinity of binding at the other end. I think that's going to be key to understanding the energetic interaction between the ions and why you get near diffusion-limited throughput with such high selectivity. You know that's probably the question that drives me now the most. I really want to see that filter at high enough resolution, and probably it is going to require dynamical studies using spectroscopy, to see how this thing moves with different ions in it.
Part 5: Psychological Wall
MacKinnon and Miller discuss what they see as a psychological wall that is crumbling with the emergence of structures from the works of MacKinnon and others. MacKinnon also raises his concerns about NIH funding and its support for structural genomics.
Dr. Miller: Let me ask you something about membrane protein crystallography right now. It seems to me as kind of an outsider having been looking in at this field for some long time, in a way a lot of feeling like a kid looking into the candy shop window, it feels like that last year with your structure emerging and Doug Rees' structure of the mechano-sensitive channel emerging with Senyon Choe's structure of the T1 domain, these ion channel structures suddenly appearing, bursting forth all around the same time, it seems to me that there is a psychological barrier almost that has been prevailing in the field of ion channel studies in general. Everybody who wanted to know about mechanisms of ion channels for the last 20 years has been thinking, "Oh, we need a structure, but we can never get a structure." And there are all these horrible reasons why it's virtually impossible to crystallize membrane proteins. Very few of them have been crystallized, and so on. And I think everybody, except a very small number of people, were simply frightened by this. But now in the wake of your structure and these others that then followed it, it seems to me that there is this a psychological wall that's beginning to crumble. Do you think that that is just a fantasy, or do you think that actually there's going to be some movement now in the future, that this acceleration is going to happen?
Dr. MacKinnon: I think it's absolutely true. I think there is a psychological wall that's crumbling. If you think about it, the small number of membrane proteins that were solved, were solved in a very small number of labs, who did a couple, and they were very well known for that. And you know, it is a hard problem. It's not that the problem is trivial, but I think that there is a psychological barrier coming down, in that there will be new methods for getting this done, as well, that we'll see in the next few years. I don't know what brings about that change, I mean practically speaking. I'm sure that if my little lab with little experience could actually do this then that's a good reason for people to believe, "Gee, these are solvable problems." You don't have to be a detergent biochemist for 30 years to be able to do this problem. And I think that with a larger number of people doing it, we'll see more and more of these structure coming over the next few years.
Dr. Miller: From where you sit, do you see more young crystallographers emerging from their postdocs beginning to be willing to undertake membrane proteins or ...
Dr. MacKinnon: They're not pouring in, actually. They're not pouring in.
Dr. Miller: It's still very risky, I would think.
Dr. MacKinnon: No, they're not pouring in. I think they view it as quite risky. Yeah, so the number of labs doing membrane protein crystallography is still quite small, and it is still risky, and I have colleagues who are working very hard and are worried. And rightly so. Because the problems are hard. And I have to emphasize that part of the difficulty is the problems are harder than a four-year cycle of an NIH grant. They are harder than that, and it has to be recognized.
Dr. Miller: And most of those problems were solved in Europe where the scientists there were not under the four-year, five-year cycle.
Dr. MacKinnon: In my view, there is a very good reason why those problems have been solved outside of the United States, right, because I think that people couldn't take the risk here. I guess I left one reality out in thinking about it. I talked about the reasoning for moving was creating a do or die situation, but also you know, I had to fund this effort somehow, to be plain and blunt about it. You know, I got a start up package that helped me initiate this effort, and then I was fortunate enough to become a member of the Howard Hughes Medical Institute. But yeah, I think it's very important that it be recognized that these problems take more than four years. They are solvable, but they take more than four years, and people have to be supported for longer than that.
Dr. Miller: Yeah, and of course that's a difficult choice when you have limited funding, is how do you know where the likely support, where the likely payoff is going to be, and so on. Do you see that there's a way to work this out within the confines of the NIH funding system?
Dr. MacKinnon: Oh, I'm sure there is, but a special effort has to be made. And I don't mean to upset colleagues to hear what I have to say, but in some ways I'm nervous about structural genomics and the NIH seeming to want to go ahead and support this. Solving membrane proteins, aside from what a few people may say or think, in my opinion, solving membrane proteins won't be served by structural genomics efforts. These kinds of very difficult problems, I think, need to be categorized specially by the NIH.
Dr. Miller: Why exactly do you think that structural genomics is not going to help with membranes...
Dr. MacKinnon: Because if the goal of structural genomics is to identify many folds very quickly, people are not going to be turning to membrane proteins to do that.
Dr. Miller: Do you think there are going to be a lot of new folds in there that haven't been seen?
Dr. MacKinnon: I'm sure there will be some... In membrane proteins?
Dr. Miller: Yes.
Dr. MacKinnon: I don't think membrane proteins are going to be fundamentally different than soluble proteins in that regard, in their folds. Yes, there'll be new folds simply because the proteins had to solve different tasks and they tend to be living in, you know, a very constrained world of a planar lipid membrane. But beyond that, I just think the difficulty of membrane proteins makes this massive approach of quickly solving structures—membrane proteins are not good subjects for that, that's all. Just for a very practical reason. Yeah, and I think that it's still going to be for a while that the people solving membrane proteins, compared to people doing structural genomics, are going to be the artisans, who care very much about a particular protein or a particular class of proteins and are willing to risk their careers on solving them.
Part 6: Further Reflections
MacKinnon offers reasons why "Aunt Gertrude," i.e., the taxpayer should care about scientific research and has this advice for young scientists: Take a risk.
Dr. Miller: I wonder if you have a speculation about a fact that I've been struck by over the last years seeing membrane protein structures emerge. And that is that every single membrane protein structure that has been solved by crystallography is a prokaryotic membrane, is from a prokaryotic organism or at least from an honorary prokaryotic like a fluroplaster.
Dr. MacKinnon: Yes, there are a few exceptions, but almost exclusively that's true. I don't know. Well, one point is, well there's beefheart.
Dr. Miller: That's mitochondria. That's an honorary prokaryotic.
Dr. MacKinnon: Okay.
Dr. Miller: I think if you actually add them up there's nothing from a...
Dr. MacKinnon: I think there's a...
Dr. Miller: Oh yes.
Dr. MacKinnon: One that's plugged in.
Dr. Miller: That's right. There are some lipases, that's true.
Dr. MacKinnon: There are a few exceptions, but you're right. I think that's largely because of availability of protein, not because of any special stability. Yeah, I think so. There may be a little more stability, but I don't know the answer to that, and I don't think that it is going to be that much more difficult, once the cell biology problem is overcome.
Dr. Miller: Of, you mean, making a large amount of a crystallographic quantity of protein.
Dr. MacKinnon: Right. There's a light harvesting complex. There's a plant light harvesting complex, as well.
Dr. Miller: Chloroplast.
Dr. MacKinnon: Okay. Yes okay, I should have listened very carefully to you (laughs). Yeah, you're right.
Dr. Miller: But certainly the stability of things like KCSA potassium channel, of the mechano-sensitive channel, and the porins, certainly those had to have contributed a lot.
Dr. MacKinnon: Thermodynamic stability, I think, is very important in being able to solve the problem. And you know for some of these, it might mean we'll have to develop some genetic screens to screen for thermodynamically more stable versions of what we want in order to really solve the problem. It's going to require a lot of resourcefulness on the part of us all to solve some of these problems, but it'll keep us out of trouble.
Dr. Miller: One of the hardest questions, I don't have to face the question very often, but when I have, it's one I always trip up on, and I don't know, I never come out with a very good response.
Dr. MacKinnon: Thank you for asking (chuckles).
Dr. Miller: So the question is, why should Aunt Gertrude care about this kind of research? Or instead of Aunt Gertrude, let's say why should the taxpayer support this stuff?
Dr. MacKinnon: It's a very good question.
Dr. Miller: I mean it's not a trivial question, but a very important one. Why should the taxpayers care whether you are having a good time seeing three ions in a row inside of this pore?
Dr. MacKinnon: It's a very important question, and you know, there's no question in my mind that ion channels are going to be very important targets for pharmaceuticals in the future. They already are in some cases. But partly, it's limited I think largely because of this parallel history of channels being studied in an electrophysiological way, rather than a biochemical way, and that's because channels are scarce. We couldn't purify a lot of them. But I think our ability to purify them, to understand their structures, how they work, is going to open new ways to treat diseases like epilepsy, cardiac arrhythmia, hypertension, asthma. I'm convinced this is going to happen.
And one might ask, well, how many diseases are related to the abnormal ion channel? And the answer to that is, well, I really don't know right now, but I do know that there are many diseases where the condition can be tuned by modifying the behavior of a particular ion channel. And so even if the ion channel isn't the primary culprit, by being able to pharmacologically manipulate a particular ion channel, we can provide therapy and treatment for many conditions that afflict us. So I think it is a very good and certainly an important question, and I think that it has a good answer. I think they are unquestionably related to health and disease in humans.
Dr. Miller: Let me finish with the last question. Where are you going in the future with your research now? What do you want to do in the next let's say—five years is infinite time for any scientist—so say within the next four to five years.
Dr. MacKinnon: You know me very well. You know my cycle. So I would say in the next four to five years, I want to see the selectivity filter at much higher resolution. I want to see its dynamics, and I want to test this specific idea that one ion talks to another through the structure of the selectivity filter. I think it's a very interesting feedback chemical device, and I want to test that idea. I would love to see the voltage sensor of a voltage dependent ion channel. So we work hard on that and have a long way to go, but I think that's going to be a marvelous thing that nature made.
Dr. Miller: You're going to go after another class of stuff.
Dr. MacKinnon: And in this case potassium channels, and those are, of course as you know well, the potassium channels that will have a very similar pore to the KCSA potassium channel that we solved. But attached to it, then, there will be the device that allows the pore to open and close in response to changes in membrane voltage. And that's central to electrical signaling in biology, and I really want to see that structure. Those are the very main questions. There is other work we do with PAS domains and on potassium channel beta subunits of voltage dependent potassium channels, and I view those as feed-ins that tune the voltage sensitive gating. So they're all part of this project to understand how membrane potential controls the opening and closing of the pore and how different mechanisms then feed in on that to tune it. So that's what I am thinking about now, and in fact, it's what keeps me excited when I get up in the morning. And I would say that I would love to be able to do this in five years. I don't know, I have probably just jinxed myself completely, (laughter) but I would love to be able to do it because I know that I do get itchy. And I also feel like if I don't really change things in a big way, then I'll get stuck in my ways, so I probably would then want to do something real different.
Dr. Miller: Well, you have a history of doing things different.
Dr. MacKinnon: Something that will make me feel completely incompetent and on the edge. That's what I'll want to do.
Dr. Miller: Some people drive racecars for that feeling.
Dr. MacKinnon: Yes. (Laughs.)
Dr. Miller: Actually, I have one more question, and maybe it's a question that won't work for you because you're too old now to be an enfant terrible, and you're too young to be an eminence grise, but could you ...
Dr. MacKinnon: (Laughing). You'll have to translate those for me.
Dr. Miller: You were one, and you'll be the other some day. But do you have any kind of advice you would like to offer to scientists emerging in this field, in the field of biomedical research, emerging from their postdocs and facing, what is, I think, to every newly hatched assistant professor in an independent lab a frightening prospect of making contributions and surviving. Not even surviving, but being satisfied, intellectually satisfied, and feeling productive in the research world that we all face now.
Dr. MacKinnon: Well, I think we shouldn't be just shooting to survive. We should be shooting to try to make a difference. But then again I don't really say that as advice because I think the people who do that, think that way, and the people who don't, don't. So you know, just take a risk. Go for it. I think if you crash and burn trying, it's still going to be better than if you never tried at all.