Albert-László Barabási is a distinguished professor at Northeastern University in Boston. In this episode, he tells us how he established the field of network science. He explains the expert’s fallacy and why it’s time to move to another field once you become afraid to break things. He tells about his strategies to select research projects with his students, and that the science only really starts after the first draft has been written. He also tells us how the crucial skill to make discoveries is to sense which idea’s time has come, and how to move into a field when you think that you can bring something all of your own to the table.
For more information on Night Science, visit https://www.biomedcentral.com/collections/night-science .
I learned not to listen to experts. I also learned to not pursue too much an area when I become too much of an expert. The fallacy of the experts is that everything seems obvious. And they cannot see what a new idea could develop to, because they know too much about it. So my modus operandi is: learn as much as I can about the problem if I have an idea what I want to do, and then leave it. I want to keep my childish excitement about the areas that I'm in. And I feel the more I know about that area, then I’m not childish any longer. I'm afraid to break things. And when you are afraid to break things, in my book, that's the time to get out.
Welcome to the night Science Podcast,
where we explore the untold story of the scientific creative process.
We are your hosts, I am Itai Yanai, and I am Martin Lercher.
Today, our guest is Albert Laszlo Laszlo, who is a distinguished professor at Northeastern University. Not too many people can claim to have started an entire research field. But Laszlo actually has done precisely that, and now it's called Network Science. What he observed back then was that natural evolved networks, such as the Internet or biological networks, they have a certain special property: they are scale-free. A few nodes in the network have many connections, while most others have actually very few. And this asymmetry happens at all scales. It drives many important properties of the networks that surround us.
Laszlo, you are what we would call a renaissance scientist, in that you've made seminal contributions to fields that are as diverse as really can be, from biology to engineering. Your original training is in physics – as is mine, coincidentally. Could that be a factor in your creativity? Maybe. I don't know. Laszlo, we think of you as a tremendously creative person that we have admired for a long time on. So it's a real honor for us to talk with you today. Welcome, Laszlo.
It's my pleasure to be here, of course, I should mention the fact that, my son, who is a PhD student at Harvard, was really thrilled that I made this podcast. Let's do something good with it!
We'll do what we can. Laszlo, I think we all agree that as scientists, we have to be creative. Does that creativity come easily to you?
It's a very complicated question, in the sense: how do you measure creativity? This is something that we struggle professionally with, because one of the research projects in my lab is about scientific success. And one of the hardest things to pin down is what it means to be creative in that space. Because you can say, hey, somebody who works in multiple fields must be creative, because how could you do that; but you can be even creative within one particular very narrow area, and come up with new and novel perspectives and solutions. So I think the creativity aspect is something that we all try for, but it's the hardest to pin down on a daily basis of what it really means.
But if we did insist on pinning you down, what would be your definition, actually, of what is creativity?
Well, it's interesting, because at the end, you have to keep the goal in mind, right? Particularly as a scientist, the goal is a product. A product could be an idea, right, but also, the product is an idea formulated in a way that can reach other individuals. The product is a discovery. But the discovery has to be packaged. And there is lots of creative work going in, not only in coming up with original idea, but also in translating it and bringing it out in a way that other people can appreciate that. And often people think, oh, creativity is that “eureka moment” when you come up with an idea. No, I often think that ideas are cheap. What is really expensive is the realization, the bringing out, the construction of that idea in a way that others can appreciate and can build on.
So I would agree, I think, in terms of ideas maybe being cheap if you think about new consumer products, for example, you can come up with all sorts of variations of existing things or new things. But in science, I would have thought the challenge is to have an idea that can answer a question that previously seemed not answerable. So can you expand a bit on this idea that ideas are actually cheap also in science?
Well, you know, I, for decades subscribed to the genius idea in the sciences or in the creative space. But the more time goes in, the less I subscribe to that. And the way I think right now about it has been shaped by a very famous paper by Robert Merton, in 1961, wrote a beautiful piece, effectively arguing that there's not a single discovery in the world that could be associated to a single individual. And to arrive to that, they went back and looked at all the major discoveries that are in encyclopedias, and that we are proud of as humanity. And then it turns out that there was always two, three or often 10 people who came up with the same idea. So a discovery is born when it's ready to be born, and when the conditions, the pre-existing knowledge has emerged in a way that could actually be articulated, that it's meaningful. And [where] your creativity, or the genius, comes in is: can you feel what is that idea that is ready to be born? And if you can, you need to be aware that you are not going to be the only one. Because when the conditions have emerged for that, many other people will have the same idea. Now, it doesn't mean that many people will be able to act on it. And that's where the interesting race comes along: can you actually act on it in a way that you will get credit for it?
Well, Laszlo, going back to this idea of are the ideas cheap, would you agree with this statement: I think what you're trying to say is that there are many ideas, they surround us all the time. And really, it's the process of selecting the idea that’s the decision that we can make for having a productive project.
Absolutely. That's right. And when is the right [time] to engage with a particular idea? Do you see a path towards articulating that discovery, to get the support for that? Well, let me give a very far-fetched idea. Would I be able to read your thoughts? Is that an idea that has been around for a while, right? And it's mostly in this esoteric space. And I actually believe that there is some science behind it. But are we ready to tackle it? No, we're very far away from it. If you would start tackling it now with the current set of tools, you will enter the esoteric set, not the science. So there are lots of fundamentally good ideas, but the time has not arrived to actually explore that. And yes, indeed, there are, at the same time, a huge number of ideas that are floating around that would be cool to actually engage with. And often myself, the questions I ask: is the time right, and do I have a tool set for that idea? Because if I think that it is now time to cure cancer, but I don't have any tools that will get me any closer to that, that idea is worthless. It may be the right idea, right? But can I contribute to that? So always, the question is not “Oh, my goodness, this is such a cool problem, we got to work on it”, and that I get always in my lab, right? My students and postdocs come up with really great ideas. And then I say: Okay, how could you – with the current knowledge base that you have – contribute to this idea? Is this something that it's good to work on, but has nothing to do with what you did before? Or you could actually make the case that what you're bringing on the table could be transformative to solve that idea?
So, now I get this idea that the way things work in your lab is that everybody, you, your students, your postdocs, come up with new ideas all the time. And then your task as the head of the lab, is to figure out: is that the right idea at the right moment in time for the right person? So it's not so much having the ideas, it's really sorting through the ideas and deciding which are the ones that we should be working on.
That's right, that's part of the project? One of them is actually to come up with good ideas. And I don't want to underestimate the value of that. So when I say ideas are cheap, it doesn't mean that we should not try to come up with ideas? But equally important is do we have a good fit with the lab’s interest, the lab’s journey, and that particular idea? And most important, do we have credibility? And the credibility really means that if I'm going to tackle that question, would people pay attention, that the tools that I bring on the table is relevant to the problem? Otherwise, we're out there in a vacuum. And to be very precise, I always tell my postdocs: listen, you need to make the case that in our case, network science, network thinking is the key to solve that idea, right? If it's not, then where's your credibility in addressing that problem? And why would you be the right person to address that? Because one thing I never believed in is that I'm any smarter than anybody else who works on the same problems that I'm trying to work on. So I cannot outsmart anybody, none of you actually out there. So if you're already working on the same problem, I don't think that I will have a major advantage on that.
And one idea that I think no one can say is cheap or small is your idea of the scale-free networks. I think that idea was so monumental, and we all need to give you a lot of credit for recognizing the bigness of this idea and the way you acted upon it. And really, in the terminology that Martin and I like to use, you exported it to other fields. You took it and you applied it to biology, you applied it to internet networks, you applied it to social networks of sexual relationships. And you were just saying that the lab’s expertise in network thinking allowed you to make these contributions. What was it really like in terms of having the credibility to go into fields that you have no training in at all, and somehow making a seminal contribution?
Can we step back a little bit, because I actually don't consider the scale free network idea as the most important one in that creative journey. I consider the network idea being the most important one. And the scale free network is just a manifestation, a product of that thinking. And since you are talking about credibility, and I know your questions include how ideas are sourced, the scale-free network concept was preceded by five years of thinking and working on networks without being able to publish anything. And that was really the pivotal moment. And let's just run back where that idea came from. I was in New York City, living in the Bronx, working at IBM. And over Christmas, I chose to pick out a book about what computer science is, and that's where I encountered the concept of a graph. And it was that moment in 1994, between Christmas and New Year's Eve, that I decided that, interestingly, networks is totally under explored as a concept. It's only existing within graph theory, but it has so many natural implications. And I decided that I will work on networks. And I wrote two papers. One of them was well-hidden as a physics paper, and that was accepted in Physical Review Letters. The other one, which was very openly network science, was never accepted by any journal. It's on the archive, but I could never get it published anywhere. And it wasn't for another five years, when we finally had enough data on the world wide web, that we could get started to get published in this area. And that's when the scale-free networks came. So scale free networks really came five years into my journey about thinking about networks. And I really consider that the pivotal idea there was networks.
So in that example that you just described, really, the most important point indeed seems to be that you found out how to show that idea to the world, so that the world would listen to it. And it took you quite a lot of perseverance in order to get to that point.
Yes. And let me just say something about that. The first five years, I was really terrible at it, because I've submitted to four different journals, that first network science paper, and everyone turned me down. And they didn't turn me down because they thought that the paper is flawed. They just couldn't understand: what is this? And looking back, what I'm realizing is that I could not articulate: what am I doing? No one questioned the math, but they questioned the motivation of exploring networks. And it wasn't until we managed to get access to the world wide web data, that, at the same time, the narrative clicked as well. So I was not only able to get real data and show, here's how this thing looks like, but at the same time, I was able to articulate it. And after that moment, in 1999, we had the next four or five papers all in nature or science, and they were all taking in different directions. As you mentioned, we took it to protein interactions, we took it to metabolic networks, we showed the network robustness and attack vulnerability and dimensionality…
It was amazing!
Right, and then eventually we went to controllability and all of these different things. But the idea behind all of that work was one word: network.
That's fascinating. And I think it's really interesting how you were telling us that your initial paper was rejected from multiple journals, because you just couldn't explain to people why this was important. It reminds me of the favorite question of my postdoc advisor, Laurence Hurst, he liked to asked after the departmental seminars: “Why is this interesting?” And it wasn't necessarily a polite question, but it was a very relevant one. If you can't explain to people why what you're doing is interesting, then they're not going to listen. And obviously, you actually figured out how to do that very well afterwards. But it seems it took you a while to do that.
Yes, it's so easy to go back and say: Oh, look at the citations, look at where this guy published and things like that. But you don't actually see how many years of struggle it took to click. I wrote this book “Network Science”. And in the last moment, just before publishing it, I decided that the first chapter will be what I call a personal journey in network science. And I described the five or six failures that I had during these five years, that I had to endure before I could get to that moment, to talk about network science.
Interesting. But you know Laszlo, I would like to propose the notion that the suffering that you endured – I'm sure you did suffer, I can relate to that entirely – but I want to challenge the notion that it was because of some mistake, that it was because you didn't know how to explain something. I think it's the process actually, that in the beginning, when you were working on network science, you really didn't know why it was interesting. You just thought it was cool. You just thought it was elegant. There was a certain attraction to it that can't really be simply explained. And only much later down the path could it emerge that this was useful in some way, that it is interesting.
I may challenge you on that. Because I could articulate “why is this interesting?” What I could not articulate is what discipline does this belong to? And that's where I had the biggest problems, right? Because the physicists at that moment felt that this is not physics, and the biologists didn't think it's biology, and neither computer scientists felt that it's computer science.
In the end it was everything.
It was everything, right? And at the end, I think by now we made the case that this is really an integral part of statistical physics, but also integral part of computer science, and of biology and so on. It's a tool set like algebra. Who owns algebra? Does math own algebra? Not really! And the early difficulty was, I remember, it's just articulating why my discipline should pay attention. So I remember one of my good friends, we were assistant professors of Notre Dame together, and he was a very good physicist, and he said, “What is this? Is this like neural networks? Or is this spin glass? What are you talking about?” And I said: No, no, no, no, it's none of those. But then I said: Well, it's social networks and technological. But he said: why would we care as a physicist about that? And I said: well, because it displays the same self-organization processes that physicist are really good at addressing, right? And we need the tools of physics even if the application areas may not be in physics. So it did not have a home, and that was the biggest problem. And where did I send my papers? First I sent to general journals, I remember I sent it to Nature and Science, and they both said no. But they refereed it to their credit, they did send it to review. And then I sent it to my traditional physics journals, Physical Review Letters, Euro Physics Letters, who were the top journals back then. And everyone rejected it, right? And again, it was bewilderment of the referees, like: what is this? And that was my failure, to really put this one within the existing paradigm. And that's one of the issues that we often face when we come up with new ideas, does that idea fit an existing paradigm? And if not, it's not a problem. But then would you have the patience and the time to really bring it there. And this is what happened in my case, that for five years, I could not get published anything but I stayed with that idea until it clicked.
The way you described this problem, it sounds like it really was a new field that had to be established, right? You started building a new field in a place where there wasn't anything before, and so there was no established community to embrace that new idea. Is that how it was?
Absolutely. And what I saw in action is when finally in 1999 our papers emerged, and then a few others, every single citation brought in a new member to the community. Virtually every single new paper that appeared on the subject in the first three, four or five years, they were all converts, people coming from different ideas and saying: this is cool, I got to work on it. And we were building the community one paper, one citation at a time, it was totally amazing.
Laszlo, I think a lot of that success can be attributed, and we mentioned this earlier, to knowing how to explain the idea, and also the implications for when you don't know how to explain the idea just yet. So I think many of us see you as a master of this: you explain it in such a way that it can be easily grasped. And I want to ask you, are there tricks that you consciously use? Do you evolve the explanation? Or maybe you don't have a conscious process for that, it just kind of happens?
About 30 iterations of every paper. And the way I often say it is, even for the lab’s papers, that I'm going to iterate over that paper until I get it, and I get every single aspect of it. And that's very interesting, because the other aspect I always tell my lab is that, you know, we work and we have a process of how we build the paper up. And then I tell them: well, from my perspective, the idea journey starts once you put the first draft of your paper on my desk. Because when we are ready to put the first draft of the paper, it means that you have the engine, that is, the idea behind the paper. But to bring out its consequences, to bring out how it connects to science in general, how it's bringing this forward, the final paper will have no relationship to what you put on my desk as a first draft. Because that's when the thinking starts. Once you have a draft, now we have what we're working with, right, this is the core idea. And that starts a different process of: how do we make this work? How do we explain it when we start explaining it? Then lots of new ideas come, of how do you dress the story up to really bring out its consequences.
Now this might be painful to the students who perhaps thought they were done because they put the draft on your desk, and now you're workshopping it a lot. Does this workshopping happen in plain sight, maybe in front of an audience, or is it behind closed doors, just you perhaps on the board with the student?
So let's just talk about how the lab is banging around? How do we source an idea? and so on. So say you are a new postdoc who just arrives in the lab, or a new student. And the first thing I always ask everybody: now you're going to spend the first two weeks just talking to everyone, and understand what they're doing – doesn't matter if you know what you want to do, right, I want you to understand everybody what they do, not only the main project, but also learn about their dormant projects. And after you're done with this interviewing everyone, and they are all familiar, because they have all done that, so they know what to expect. Then we sit down and say: Okay, well, tell me what really interests you. And then we start a conversation about what are the labs projects that are kind of dormant that may need somebody to work on, and also understanding where your skill set is.
Yeah. So you said a major creative step is when you choose the project, when you decide, you know, this is going to be a good project. How do you choose a good project? How do you decide this is something we should work on?
Well, I have actually a long list of projects that I always source, and some of them are on my project list for years before I feel like I found a good match between the person, his or her motivations and experience, to do that. And let me give one example. Many years ago, I was in Minnesota giving a talk in a math department. And you do what you normally do, you actually start talking with all the faculty. Somebody who ended up on my schedule was a control theorist. Never heard of control theory before. And I said: okay, well, what do you do? And he was really patient, he started to explain what control theory is. He used the bicycle example of how you control a bicycle, and why you can go forward with the bicycle and why can you cannot go backwards, that you lose the stability and you cannot control a bicycle if you're trying to go backwards. And I thought: that's very interesting. And he started to show me the math. And I realized it's actually a matrix condition that you're trying to satisfy when you try to look at controllability. But networks are actually all about matrices. And then I said: that's a very interesting idea. So maybe then there is a connection between network science and control. And it's very interesting that we don't know how to control a network, not only that we don't know, but no one is asking in network science the very question: can the network be controlled? So I realized that we lacked the thinking about control in network science. But that wasn't enough, because I don't know anything about control theory, and didn't even know where to start. So, one day, I was having lunch with a colleague of mine from MIT, Jean-Jacques Slotine, and he was interested in nonlinear systems. And I asked him: do you happen to know anybody who is a control theorist? And he turns to me and said: “I am a control theorist!” He's French, you know. He said: “I wrote the book, I wrote the most popular control theory book about nonlinear control!”
Shame on you for not knowing that.
That's very interesting. So then I told him this idea. And he said: You know, it's a feasible idea no one has actually worked on that problem. But having a colleague who works on it, at least in my book, was not enough. I needed somebody in my lab to kind of develop that. And it took another two years for young Julio, who was just coming with a physics degree from Urbana Champaign, to join my lab. And he was an unusual hire, because he had no experience in network science before. He was a statistical physicist. But he seemed very smart. So I said, Great, you don't know anything about networks, nor you do anything about control? How about network control being your project. And he took it up. And he ran with it, right. But he seemed to have had the right kind of attitude and the right mathematical knowledge and everything, that I felt like he would be the right person. So that project was sitting on my to-do list for about two years until somebody joined my lab who I felt this was a good fit.
So, really, what you've told us is that you talked to a person who was in a completely different field from one that you know, control theory. And the second you could reframe his idea into network thinking, you could have an idea. So really, do you see yourself as someone who throughout their career is driven by a central idea? Like you have one big idea, and as soon as you can reframe anybody else's field into that idea, then immediately you have this idea generation mechanism.
Well, let's talk about network control. Why was that a good idea? Because, first of all, it could be formulated in two words, in a way that you almost got it once I say it, right, number one. Number two, it was addressing a real problem that we scientists learn how to analyze, how to measure it, how to build predictive models. But really, if you understand the system, you know how to control it. And that line of thinking was totally missing from network science in general, right? No one was before even mentioning the word control in the context of networks. So it was an area that no one was working on. I thought, it's a great idea and could have so many ramifications in so many different areas. And I could see a two to five year pathway for me that I can work quietly on it. without anybody breathing down my neck. It was a simple idea whose time has arrived, the tools were sitting around. And we just had to put it together, number one. And yes, we had to have a discovery. And we did have a discovery, because we ended up mapping this network control problem into a well-known graph theoretic problem. And with that we managed to accelerate the process orders of magnitude. So there was a technical advance as well. But I always say the technical advances come once you know what you're trying to do. And that's why I say my biggest idea wasn't scale-free networks. It was networks. The scale-free part is a technical advance of the journey. And in the case of network control, the idea was network control, that it is the right moment to think about how you would control the network. And the rest is details. Yes, of course, you have to bring it out and you have to make a discovery that is worthwhile to pursue. But if you know what you're trying to do, sooner or later, if you stay with the problem, that discovery will occur.
So Itai and I, we wrote this piece for genome biology where we introduced this idea of “experts dilemma”, meaning that there are some people on one end of the spectrum who are a specialist on a very tiny sub field. And then on the other end of the spectrum, you have people who don't really know anything in detail about specific fields, but know a lot about different fields. And we have this idea that probably, there's a sweet spot somewhere in the middle, where you know quite a bit about one thing, but you also know a little bit about several other things. And it sounds to me that your network thinking is actually somewhere in that sweet spot, because you know a lot about networks. But then you apply them to things about which you know not so much maybe. So do you think that's an accurate description of your research?
Perhaps. I mean, I think as a concept, it makes sense. But I also think that, in my case, this happens a little differently. When I went into control, I did learn control, I did actually read Jean-Jacque Slotine’s book and a bunch of other things. And momentarily, I became an expert in the field. But I also see a fallacy of experts. And I had experienced it as a student as well. I remember that one of my first great ideas came when I was an undergraduate. And I went to my advisor, and I said, I have this idea. And he said: Oh, this doesn't feel to me, it feels obvious to me. And I don't think it's going to get you there. So he kind of dismissed the idea, that it's not worth it to pursue. And two years later, somebody did it and totally changed the field. This was before networks. And it totally changed the field. So since then, I learned not to listen to experts. I also learned to not pursue too much an area when I become too much of an expert. The fallacy of the experts is that everything seems obvious. And they cannot see what a new idea could develop to, because they know too much about it. So my modus operandi is: learn as much as I can about the problem if I have an idea what I want to do, and then leave it. And leaving means that in my lab in the last 30 years, we have closed research areas we were really well known for. And I do so because I feel once I know too much, I'm not creative any longer. I'm not wondering any longer about the problems. I lose my ability to be excited about problems if I know too much about it, number one. And we leave certain areas because I felt like the tool set that we brought to the problem has reached its limitations. And now we're not needed any longer. And I can be very drastic at leaving fields. I remember when finally in 1999, I managed to publish my first paper on networks. When the paper was accepted, I went back to my lab of about six people at the time. And I said: some of you are doing material science, that is paying the bills, some of you are already kind of started with networks. I have some bad news for the material science. It's over, we're not going to do more material science. So you can choose to finish what you're doing and graduate, or you can join us in the network space. And just at that moment, I got a grant from the NSF to do another project on quantum dots and material science. And I called the program manager up and I said: I'm sorry, can we do something else with this? Because I'm not going to do this anymore. He said: What do you mean, I’m not going to do that? Well, I'm sorry, you know, I'm not interested anymore in this problem. But I had this other idea, and would you allow me to kind of do that? And he said: No, Laszlo, I'm sorry, I can't allow you to do that, because this was refereed, you have to perform on that. So I sent the grant back to the NSF. And I couldn't get a grant for another three years on networks. And I did so because I didn't want to be distracted anymore with that problem. I wanted all my energy to be on this new problem. So I want to keep my childish excitement about the areas that I'm in. And I felt the more I know about that area, and I'm not childish any longer. I'm afraid to break things. And when you are afraid to break things, in my book, that's the time to get out.
Wow, Laszlo, I think that was very deep, what you said about experts, that, to them, things seem obvious, when actually it's a new idea. Maybe they forget that the hallmark of a new idea is that it sounds obvious, but actually no one has said it before. And I'm really inspired by what you said. It's I can really relate to that: once you're too deep into a field, you become a little bit less creative, you need to move on. I have a question for you about that, though. Do you think that notion is something about your personality, or does it scale to everyone? In other words, maybe in science, of course, we should have textbooks and fields, but any individual should not reside in just one field, that all of us should move around constantly? Or is that maybe just your personality, and there should be other kinds of personalities that do stay in the same field throughout their career?
I often think that every healthy field is really like an ecosystem, where everybody has a different role. If everybody would be like me, we would not have an iPhone, right? Because you need people to take that idea and perfect it and turn it into a device.
It takes a village.
Yes, it takes a village. And it's really that heterogeneity is the key to that process. So no, it's not a good idea that everybody should be acting like me, this is something that worked for me, this is a method that I perfected in my lab. And it only works if there are others who bring a very different perspective on that. And that's what's healthy about science, right. That's why science can make advances, is because there is this heterogeneity of the way we come to these problems that coexist within the discipline. And we have to cherish even the people who take one idea and then work for it for 30-40 years. That is just as valuable as I am, who is trying to always source new ideas. And we all have our very important role within our disciplines.
Yes, science really thrives on that diversity, on that intellectual diversity.
Although I would say, I absolutely agree that science thrives on that diversity. But I do think the experts get the lion's share of the credit oftentimes, and we could improve the culture of science if we embrace more the people that do move from field to field, even though they don't have the right credibility – we give them a little credibility.
Well, it's complicated, because yes, the experts do get the credit in the short time. But in the long term, it’s the source of ideas that really matters. And that is not always the expert. Many, many ideas, famous ideas in science are coming from people who are outside of the field, and they become inside of it and become adopted by the field. Always my favorite example is de Broglie, right? The physics Nobel Prize for the wave like nature of particles. Is it obvious to everyone that de Broglie was a historian? No. He had no physics training whatsoever. And his brother was a physicist, and talking to him, he said: well, you keep talking about these things having waves, Why can't the particle have a wave? And he said, well, because they don't. So then he wrote a thesis, saying particles could be waves. And he was right. You know, there are many examples like that. I mean, even the background radiation, you know, the evidence for Big Bang, the Nobel prize went to two engineers who just were at AT&T, trying to perfect the radio, and they kept getting this noise. And they finally turned to some physicist and said: can you tell me what is this noise? Because we can't get rid of it, and we tried everything. And they said: Oh, you just discovered Big Bang! So those were experts in their own area. And they pushed their expertise as far as they could, in this case, to get rid of the noise, only to realize that they actually discovered something. So there is a huge room for experts. And yes, in the short term, experts have lots of authority. And we always, as authors of research papers, are disheartened when the experts come in, and they say the final thing about your paper, and that doesn't agree with your opinion. But I think that people who are kind of moving through the fields successfully, in the long run, they do get the credit for that.
So I think that's a beautiful last statement to round off this episode. Laszlo, that was really, really interesting.
Thank you for having me. Super interesting, Laszlo, I'm going to be thinking about what you said for the rest of the day. It was really profound. Thank you.
Thank you. Thanks, guys, for doing this podcast and bringing these ideas out. These are the type of things we don't often talk about. We talk about our papers, but not as much about the process of how we arrive to that. And when the most read chapter of my textbook is that first chapter that tells my many failures, and I hear from lots of students and other people that's really the most exciting part of it, I realized we need to have a venue where we talk about it. It seems like you are providing a venue for that.
Thank you for saying that.
Yeah. Thank you so much.