‘Good Scientists Solve Problems, but Great Scientists Know What’s Worth Solving’

Abhay Ashtekar. Credit:

Abhay Ashtekar. Credit:

Abhay Ashtekar is a theoretical physicist and the founder of loop quantum gravity, an increasingly popular branch of physics that attempts to unify quantum mechanics with Albert Einstein’s theory of general relativity (which celebrates its centenary this year). Currently the Director of the Institute for Gravitational Physics and Geometry at Pennsylvania State University, Ashtekar spoke to Nithyanand Rao and Swetamber Das at IIT Madras on October 7, 2015 about his inspirations, his encounters with Subrahmanyan Chandrasekhar and Roger Penrose, work on gravity and cosmology, and his criticisms of string theory.

The freewheeling interview has been edited for clarity and divided into four parts:

  1. Getting started on gravity and cosmology
  2. Learning from Chandra
  3. Challenges in loop quantum gravity
  4. Arrogance in string theory

Part I – Getting started on gravity and cosmology 

How did you get interested in gravity? Since the very beginning you have been working in this area.

Well, I grew up in a small town and not in a big city. My father was in the civil services and he was transferred to a small town called Kolhapur. There, somehow I managed to find some books by George Gamow. Now, I don’t know how. That was very interesting for me, particularly this book called One Two Three…Infinity. That had some cosmology that Gamow had written about in a popular manner. That’s what got me interested in this kind of science.

Then, I went to Bombay to do the last two years of my B.Sc. At that time, I was very fortunate that some senior professors at the Tata Institute of Fundamental Research (TIFR) started a project in which they were to get a few students from colleges – undergraduates – to come to TIFR once a week to discuss things. So inspired by Gamow’s books and things like that, I tried to construct some cosmological theories – like how Newton’s [gravitational] constant was changing in time and if that happens, how does the cosmological scenario change? I have to say that Gamow’s were semi-popular books. They were not serious scientific books but still there were a few formulae in it, so I just used that.

Then, there were people like S. M. Chitre – he retired many years ago but is still active and lives in Bombay. I gave him the paper and he encouraged me very much.

When you went to the US, you were specific that you wanted to work on gravity…

Yeah. In those days, there was no internet. It’s impossible for you to imagine! [Laughs] Therefore, one did not have too much information. So one had to go to the United States Information Service which was in the US consulate. They used to have these little brochures from various US universities which described their graduate programs. So I looked up graduate programs there. There were two – one in Maryland which had a strong program in gravity, general relativity and cosmology; and the second was in [the University of] Texas. So I applied to these two places.

Maryland wrote back immediately saying that they don’t consider students from India until they finish their Master’s, but Texas admitted me and gave me an assistantship. Probably this was due to the letters I got from various people at TIFR. But it worked out. I was extremely under-prepared as you can imagine.

So you went right after your B.Sc.?

Yes, I was not quite 20, I think, when I went. I had what was more like a sophomore-level of preparation, but I was in a graduate program. The first year in particular was extremely tough; I had a lot of work ahead of me to catch up, that was very hard. These were quantum jumps. In a way it was also helpful, because I did not have time to get a culture shock as I was too tired to do anything other than work!

Also, the people at TIFR had suggested we all go through the Feynman Lectures on Physics, which were more fresh at that time. There were problems to be solved at the end of each chapter. There was one particular problem – nothing really profound – in the first volume itself. I did the problem at first and my answer matched with the answer given at the back of the book. Then I realised that something was wrong with the answer conceptually. So, I re-did it and I got a different answer. I presented that at TIFR; they said yes, this is right. And then like an aggressive, cheeky kid, I decided to write to Feynman, saying there’s a mistake in the book – it was not really in the book, just in the answers. I wrote that if you do the problem naively then you get the answer given at the back of the book but, in fact, it’s wrong and it should be done this way.

He was very kind – he replied. He said, yes, the book is wrong and you are right. So I think that letter probably helped me later to get an assistantship and admission to Texas, even though I was not prepared at all. Anyway, I caught up in a couple of years.

That must have been a huge morale booster for you.

Yes, it really was. Feynman was very kind to young people but he also wanted to put some distance – he ended the letter by saying “you know the subject well enough to rely on yourself”. Basically telling me not to bother him again! [Laughs] At least, that’s how I understood it.

Then, I started working with a young faculty member at the same time that I was doing these basic courses [at the University of Texas]. His name was Robert Geroch; and Chandra [Subrahmanyan Chandrasekhar], was actually very impressed with him. He offered Bob [Geroch] a position in Chicago. Bob offered to take me with him to Chicago. So I finished in Chicago.

Part II – Learning from Chandra 

Subrahmanyan Chandrasekhar. Source: YouTube screengrab

Subrahmanyan Chandrasekhar. Source: YouTube screengrab

I guess you took classes by Chandra as well.

Yes, I came to know him quite well. I was very fortunate. After my Ph.D., I went to Oxford to work with Roger Penrose. That was also because of Chandra. But then they asked me to come back to Chicago. So I went to Chicago again. Particularly in this second stage, I came to know Chandra and his wife very well. They were kind. They used to invite me for dinners and so on. Chandra was so reserved; he was god-like, a completely different level of human being. But then he would get into the flow of things and he would tell all the stories – his memory was just phenomenal; there is nobody who comes anywhere close to him. He would remember what he was doing in, say, August 1931 and what had happened then. He would recall it with all the details – all the people and all the names and everything. I have trouble remembering what happened yesterday! He would tell these fantastic stories.

I was really fortunate that I got this exposure to three great people, my great teachers: One was my Ph.D. advisor Robert Geroch. Chandra told me that he felt that except for John von Neumann, he has never seen anyone as brilliant as Bob; and it was true. Bob is extremely brilliant. But then something happened and he suddenly stopped working. I don’t know what happened but before that he was totally off-scale. He had such clarity of thinking, such crispness. I learnt by osmosis – the way of thinking, how to think from scratch. He would take us once a week for a pizza dinner or something and hand us a new research paper. Those days, everything came by mail because there was no arXiV or anything. We were supposed to look at the abstract of the paper and try to guess what it was about and how did they did it. That was very good, because you have to start from scratch and you didn’t know much to begin with; and we were just graduate students. He used to put us in this situation – it was like being thrown into the water and being asked to swim.

With Chandra, I got this deeper sense of values – which is about what is “right”, a moral compass about how to be a good scientist and a good human being. A proper sense of values. Chandra was the one who said that I should go to Oxford for my postdoc. I was fortunate again as I had got several offers but Chandra said I should go to Oxford, so I went there.

I went to Roger Penrose. With Penrose also, it was really unique. He was not as brilliant as Bob Geroch was, or as quick. But he had this way of dreaming, looking into the future, groping in the dark and coming up with completely unbelievable ideas. That’s also something that you cannot learn from a book – you see these people in action and you learn. I think with all these three people I learnt things which I could never have learnt from books. Robert Geroch’s clarity, crispness and speed; with Chandra the backbone, the hard and deep stuff which always makes life meaningful; and with Roger Penrose it was a dream-like quality that is so essential for research.

The hardest thing about research is always – I tell this to my students and postdocs – this balance. When you do something and you are in the middle of it, you need – like Chandra said – a certain amount of scientific arrogance. There’s nothing wrong about scientific arrogance. There’s everything wrong about personal arrogance. Scientific arrogance is basically the belief that, yes, I am going to solve this problem. Even if other people have thought about it, it doesn’t matter; I will solve it. You really have to get into it. You want to get into the details, you want to understand the intricate structure which is laid out in front of you, find the missing links. And things that are completely wrong in your thinking and maybe also in other people’s thinking. At that time you just have to be an extreme optimist. You have to believe that it’s going to work and completely disregard scepticism from other people. But then once it is finished, you have to turn around 180 degrees and you have to look at in “cold blood”. Does it even make sense? And then poke every possible hole in it. It’s just the opposite of what you first did. First you make progress, do things; and then be your worst critic.

These two skills are draining. You can go with the first skill quite a bit, but after a while you don’t advance. You need to have this ability of really going back and looking at things critically and seeing the solidity – and poking every hole that anybody else can poke. If you don’t have this solid foundation, you cannot build on it further. You can just do the first things and not go much further. I think that psychologically and mentally this is tiring, to be able to go back and forth.

One has to be able to cope with frustration as well.

Yes, it can be frustrating because you believe in it, and you have spent so much of energy and passion and time on this problem. But then, you have to get used to it and work on the next problem. This is the skill. This is, I think, how you achieve good productivity on a long range.

The other important thing is that – I learnt this from Chandra more than anybody else – many people can solve a problem. I mean, I can solve many problems even more elegantly than Chandra might have solved. But the skill is to come up with a problem – to come up with the right problems. Things that are going to change the direction. Things that are not going to be only incremental progress but really could make a difference. And that, I think, is not easy. That is what distinguishes great scientists from good scientists – the ability to really spot this, what is really worth working on. I don’t mean to trivialise the second ability, which is the ability to solve a given hard problem, because it requires both the arsenal of tools and some brilliance. But it’s not the same as coming up with the right questions to ask. That is, I think, something that students should be aware of. It is not enough to be extremely smart and to be able to solve a problem. That is a different skill than things that will shift paradigms. Of course, you need both of them to make real progress.

You won the first prize for an essay from the Gravity Research Foundation back in 1977.

It’s a funny foundation. It started in a slightly crackpot-ish manner. But then very senior scientists like Bryce DeWitt, Roger Penrose, Stephen Hawking all submitted essays. The essays were supposed to be about ideas more than just technical papers. Something which is more important than just a technical result, something which looks at a problem in a certain way, a new direction – not paradigm-changing, not that big.

You had completed your Ph.D. by the time?

Yeah, I was actually on my second postdoc at the time. I think I was in Chicago. I had some ideas and I wrote it up. I had done my homework by seeing how to write those things so that it makes an impact. Because even if you have a good idea, if you don’t put it in the right way it doesn’t have the same impact as somebody else who might have a lesser idea but puts it in the right framework and makes interconnections. It was not something really great, but it was satisfying to be recognised. I think it’s not very often that people who are postdocs get it. Usually more senior people got it.

When we’re young and try to do something new, it’s always there at the back of our minds, how well will it be received by the experts.

Even for a technical paper, the title and the abstract are really important even if you may think “what’s the big deal?” But those things are important. Somehow those are the skills that you don’t always learn. Maybe because your advisors never tell you. But it’s important. The number of people who’d actually look at that paper would depend on how you write these things.

So yeah, it was good. I got it somewhat early compared to some other people.

Part III – Challenges in loop quantum gravity 

If we can now come to loop quantum gravity, which you’ve been working on for a long time.

It is a fact that unifying ideas from general relativity and quantum mechanics has been a long-standing problem. The motivation for loop quantum gravity comes from multiple directions. Technically, it had to do with these ideas that Penrose had about twistor space. When I was a postdoc, I learned twistor theory. Though I never worked on it, I learned completely about what was happening at that time. The big breakthroughs happened around that time in twistor theory. They’re happening again now, but there was a little bit of a quiet period for a long time. And there were some critical ideas that Penrose had, about what the role played by helicity or self-duality was. That is to say, there are some symmetries of solutions of Einstein’s equations [of general relativity], and Penrose felt that this symmetry has to do with duality. For example, if you have a photon, just like every zero rest-mass particle, it has two helicities. It is spinning either in the direction of the four-momentum or in the opposite direction. So you get these two helicity states. The same thing is true in the weak-field limit for gravitons. So Penrose was trying to generalise that idea in the nonlinear context.

I felt that the way that it was happening in twistor theory was very, very interesting, but that somehow it was not going completely in the right direction. They were emphasising complex manifolds a lot, and not real manifolds. I felt that one has to take those ideas but formulate them in terms of real space-times, real metrics. Because that’s what we experience – it’s more directly, physically relevant. I felt that there was some deep idea but it was not being used in the most fruitful way. That was the one technical aspect of the problem. So one deep motivation came from some of the important ideas from twistor theory and, as I say that, they’re becoming important again now.

The second thing was about the idea that, because gravity arises from the space and time in general relativity, if you have a quantum theory of gravity it should also be a quantum theory of geometry. Therefore, this continuum geometry we see around us should be an approximation. Just like this table, for example, looks very smooth and continuous to me. But if I look at it under an electron microscope, I see there’s this discrete structure – there are atoms in a lattice, and there’s a lot of vacuum between them. So the idea is that there should be atoms of geometry, that there should be some fundamental building block out of which geometry arises. And then, coming from these ideas that I was telling you, which were inspired by twistor theory, it turned out that the fundamental excitations of the geometry should not be like gravitons but it’ll be deeper. Gravitons will be an approximate concept later on. But it’ll be deeper and they turn out to be one-dimensional.

Abhay Ashtekar. Source: Abhay Ashtekar

Source: Abhay Ashtekar

So the fundamental excitations are one-dimensional, which is a little like a polymer. If I take this shirt, and I take a magnifying glass, I can see that the shirt is fundamentally one-dimensional, because the threads are one-dimensional. It’s just that those threads are so densely packed that I get an illusion that it’s two-dimensional. What comes out in loop quantum gravity is that the geometry of space is like that. It’s woven by these one-dimensional fibres, it’s like a polymer. But this polymer is so intricately woven and tightly spaced that we get this illusion of continuum. It’s coarse-graining. If you go to the atomic size, it’s not continuum at all. But if I coarse-grain it, there are so many atoms that, for all practical purposes, it’s a continuum. The same thing is true of geometry. The geometry we use in Einstein’s theory, general relativity, where space-time is a smooth continuum, is an approximation. To go beyond, one has to work with this fundamental building block, these atoms of space-time. That’s the basic idea of loop quantum gravity. Then one has to come up with proper equations for this.

In the 1990s, several colleagues, particularly Jerzy Lewandowski at Warsaw – who was a postdoc with me – developed this quantum theory of geometry. Since then, it has been used for black holes, for cosmology, the Big Bang. So there are about 250-300 people in the world who work on this now. We have meetings called Loops every two years – just this year we had one, in Germany.

Do you foresee any experimental tests?

In any approach to quantum gravity, experimental tests are hard to come by, just because technology has not caught up with the theory. I mean, general relativity is a hundred years old, and it’s only now that we can hope to see hard tests of general relativity. We still don’t have a single hard test of the strong field regime of general relativity. All the tests we’ve had are more or less about weak gravity – strong compared to Newton’s, but weak compared to Einstein gravity. The hard test would be two black holes colliding and they’d produce gravitational waves. There’s great excitement now because the gravitational wave observatory [Advanced Laser Interferometer Gravitational-Wave Observatory] has come online. They’ve been building for 20 years, but now they have the sensitivity to be able to see this. There’s this rumour that there’s a detection. We’ll see what happens.

So even with general relativity, it has taken so long, a century. Quantum gravity is even harder to test. Therefore it’s not likely that we’re going to get direct tests of any quantum gravity theory tomorrow, but we would have observational evidence coming in. And that would be through – to me at least, it seems – cosmology, the very early universe. In the last three years, we’ve been working very hard on that, trying to push the so-called inflationary scenario. Inflationary scenario starts very early when the density of matter was extremely high, but still very low compared to what’s called the Planck density where quantum gravity effects would come up. It’s about 10-12 times Planck density. Planck density is about 1097 kg/m3. So the density relevant for inflationary cosmology is 1085 kg/m3. Nuclear density is only about 1018 kg/m3.

So we’re already talking about around 70 orders of magnitude higher than nuclear density. But we want to go even beyond – it was very hard work, but very satisfying also. It’s like what I was telling you before – during those years, you just have to believe that somehow it’s going to work. We did succeed, we did complete the program.

So you’re essentially looking for the signatures in the cosmic microwave background (CMB).

Exactly. But it could also be large-scale structure [in the universe], ultimately. It’s amazing that this large-scale structure arose from the CMB. There are limitations as to what you would be able to see with CMB and what large-scale structure can show you. It’s just the CMB structures that have got magnified to the large-scale structure and, therefore, looking at galaxy-galaxy correlations and such things, it really came from some correlations of the CMB. So, the inhomogeneities [of the CMB] – there will be some deviations because of the pre-history, which is even before inflation – have to do with quantum gravity. Then the question is: are they observable or are they not observable?

I have been working on it for so long and now one can actually make contact with observations and say that there should be deviations from what the standard inflation is and these deviations would be the imprints of what happened before. And that has to do with the Planck epoch and quantum gravity and so on. We are still not in the stage in which one would say well, this is the smoking gun. Even inflation is not the smoking gun of anything. People would say that there are other scenarios. There isn’t any other obvious explanation which works so well, so one takes it very very seriously. Similarly, there are these deviations from inflation, for which there should be some natural, fundamental explanation.

So, with improved observations, it should be possible to have experimental tests.

Yes, in fact Planck [a European Space Agency satellite that studied the CMB] data may be useful. The Planck collaboration is now going to release the data that we need. They plan to release it within a year from now – in the middle of next year. So, these are interesting times!

Part IV – Arrogance in string theory 

Strings and stars. Credit: yogomozilla/Flickr, CC BY 2.0

Strings and stars. Credit: yogomozilla/Flickr, CC BY 2.0

There was this Strings conference recently at Bangalore. A claim was made there, in fact quite explicitly, that it’s the only way to quantise gravity and so on.

There are many things I have to say. First of all, I think that string theory has really enriched our understanding enormously, especially with new connections in mathematics and this so-called AdS/CFT correspondence. In some sense, it has expanded the reach of Einstein’s gravity because you can use methods from gravitational physics – for example, some Green’s function on black hole background space-time – in order to calculate some quantities in superconductivity. It’s pretty amazing that you can do such things. Of course, hard condensed-matter physicists will say while that’s useful, it’s a model which mimics superconductivity at some level but it really is not high-temperature superconductivity we actually see in materials. I think, say, 80% or 90% of the condensed matter physicists would say that. But to me it is still interesting that one can actually do such things.

So there is no question that string theory has enriched us. What is unfortunate is that they are extremely intolerant, in my opinion. It’s everywhere. There is no need to be so intolerant. Because in science there should be a competition of ideas. Let it be a free competition of ideas rather than declarations. It’s not faith; and somehow when you say this is the only true thing, I don’t see much difference between that and some guru saying that his is the only true path.

One of them even made a claim that alternative approaches have been incorporated to string theory and, therefore, it’s the only true theory.

Joe Polchinski, a very prominent string theorist, he did say explicitly that – this was some years ago, at KITP [Kavli Institute of Theoretical Physics] Santa Barbara at its 25th anniversary. He said, well, string theory has incorporated everything. String theory is a little like Microsoft because at that time Microsoft was incorporating everything. He said loop quantum gravity was more like Apple. I thought it was a great complement! [Laughs] He explicitly said so. I said somehow I could accept Apple; at least Microsoft wouldn’t gobble us up!

That was a huge compliment.

Well, yes. In retrospect, it was a huge compliment, exactly!

String theory has achieved a lot. I don’t know why science needs such statements; indeed, scientists should not make such statements. Let the evidence prove that it’s the only theory. Let the evidence prove that it is better than other theories or let its predictions be reproduced more than those of others. Science should not become theology. And, somehow such statements have a strong smell of theology, which I don’t like.

There’s even been talk of “post-empirical science”.

Yes. There was another Strings conference in India at TIFR, in 2001. I happened to be in India at that time – people had just discovered that the universe is going through accelerated expansion, so that the cosmological constant may be positive. And I saw in newspapers that Tom Banks and Edward Witten had said that, no, the cosmological constant cannot be positive because it is incompatible with string theory. It has to be negative, they said. And that these observations are premature. They were completely wrong. The fact is that nobody goes back to these things and says, well, let us be a little more modest about it.

It’s like shifting the goal post.

Exactly! There is nothing wrong with making the statement. But then ignoring completely that you made that statement – that is wrong. And then to say that this is the only theory. It has not had hard experimental/observational success, and it has not made that much progress in quantum gravity. It does not tell us, for example, what really happens when a black hole evaporates. There is some dual description of it but there is no space-time description of it. It doesn’t tell us what happens to the singularities of general relativity. All the hard questions that are there in quantum gravity, they are not answered by string theory.

The second thing is that, in fact, the big progress of string theory since 1997 – with Juan Maldacena’s conjecture, AdS/CFT; so, it’s now been 18 years or so – has been in the applied ideas of gravity to other areas of physics and there it has been successful. I am impressed by the success. Other people who actually work in other areas may not be as deeply impressed but I feel that to have seen an underlying unity in science at some level, even though it is not at an exact level that one wants it to be, I think that is good. That’s progress.

We seem to be using these gravity ideas in other domains of physics rather than solving quantum gravity problems. I don’t think that the quantum gravity problems have been solved. And I have said this explicitly in conferences with panels – in which Joe Polchinski, Juan Maldacena and I were panellists – that, in my view, this is very powerful and these are good things. However, the AdS/CFT conjecture is the only definition of non-perturbative string theory one has – and it’s a definition, it’s not a proof of anything. It talks about duality, but there’s no proof of duality. To have a duality, A should be well defined, B should be well defined and then you say that A is dual to B. Since we don’t have another definition of string theory, we cannot hope to prove that string theory is dual to its conformal field theory. You can define string theory to be the conformal field theory. You have to construct a dictionary relating string theory in the bulk and conformal field theory on the boundary. That dictionary has not been constructed in complete detail.

Again, nobody is taking anything away from the successes that the AdS/CFT duality has had; but there is a big gap between the successes and the rhetoric. The rhetoric is at a much higher level than the successes. So, for example, in this conjecture, first of all the space-time is 10 dimensional. The physical space-time is supposed to be asymptotically anti-de Sitter, which has a negative cosmological constant. But we look around us, and we find a positive cosmological constant. Secondly, the internal dimensions in the conjecture, or this definition, are macroscopic. The Kaluza-Klein idea is that there are higher dimensions but because they are all wrapped up and microscopic, say, at Planck scale, we don’t see them. That’s plausible. But here, in AdS/CFT duality, they need the radius of the internal dimensions to be the same as the cosmological radius. If so, if I try to look up I should see these ten dimensions; I don’t. So, it can’t have much to do with the real world that we actually live in. These are elephants in the room which are not being addressed.

There is a Centennial volume of General Relativity which was just published. I was editor-in-chief of that work. The volume has four parts – the fourth part is called Beyond Einstein and deals with quantum gravity. At the beginning, there is an introduction for a general audience, a not-too-technical introduction as to how the field of quantum gravity has evolved. There’s a subsection called “Elephants in the Room” and I say explicitly that there are these obvious issues and practitioners just pretend that they don’t exist. And that to me is unconscionable; I feel that that’s not good science. I don’t mean to say string theory is not good science, but publicizing it the way it’s done is not good science. I think one should say what it has done, rather than this hyperbole.

What did you think of Lee Smolin’s book The Trouble with Physics? I believe you’ve worked with him.

I’ve worked with Lee but I have not read that book. That’s a qualifier that I have here. Some of my close friends who are very good physicists who have read the book – who are not in gravity, but very good condensed-matter physicists – said that they liked it. They thought that he made good sense at the end. But string theorists say that the book is misleading, it has wrong or false historical statements. I don’t know because I was not there. So, I don’t know much about that.

I feel it’s very good that people like Lee, who understand things, write such books expressing their point of view of it. But personally, I feel that I would like to do science. Let its value be decided by what comes after – maybe it’s not worthwhile. That’s fine. I had a good time, and somehow that’s enough for me in some ways. But I do believe, as I told you before, that I wouldn’t be spending so much energy and time and concentration unless I believe that it has some very good ideas. I firmly believe that whatever the final theory is – it’s not going to be loop quantum gravity as we know it today but it would have some essential ideas that come from loop quantum gravity; it would probably also have some essential ideas from string theory – I certainly think that the idea of quantum geometry is going to survive. It is going to be there. It might be much more transformed, but it is going to be there.

So, I feel that I personally don’t want to get into these debates. I would like to talk more about doing science.

Nithyanand Rao is a freelance science writer based in Bangalore. Swetamber Das is a Ph.D. student in the Department of Physics at IIT Madras.

  • TD

    Thanks for publishing it. It is fascinating to read about the views of one of the foremost theoretical physicist of our time….

  • V. Balakrishnan

    Thank you for publishing this wonderful interview with Prof. Ashtekar. It is most enlightening, and should be read by all scientists, and not just physicists. Prof. Ashtekar’s insightful remarks in the section ‘Learning from Chandra’ are particularly germane to all researchers. An excellent and memorable piece!

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    Money is the most important problem to solve, because it affects every person every second of every day.

    What is “solving gravity”? Creating an anti-gravity machine to escape earth?
    What is “cosmology”? Finding a place to escape to?

    People with money:
    1. do not want money to be solved, and
    2. want to escape earth.