2023

This year is almost over. So, I want to reflect on what I did this year. At this point, the major emotion I feel about this year is humility. I want to think about what I did a very bad job, and what I really want to do better next time. Probably I should also add this to my cv of failure. 

• I want to start out with something I somewhat regret.
  
  This year, most of my focus was on learning how to do string loop computations in Calabi-Yau orientifolds. This is still an ongoing obsession. This obsession started shortly after the publication of https://arxiv.org/abs/2107.09065, as it became very clear that without computing \alpha' and g_s corrections explicitly it would be very hard to convince people that our vacua are well controlled. I felt this way, because every time I talked about KKLT and our attempts to explicitly construct such solutions I was drawn to lengthy discussions about \alpha' and g_s corrections. Basically, there was an unanimous understanding that someone should compute \alpha' and g_s corrections.
  
  Despite the consensus that computing \alpha' and g_s corrections in Calabi-Yau orientifolds is a very important technical problem, it was very difficult for me to find a collaborator to work on this problem with me. I think I tried to find a collaborator for almost a year after the publication of our small cosmological constant paper. After certain point, I think it became quite clear to me that probably I will have to work alone on this problem at least for a while.
  
  For quite a while, of course, I made no progress, as I had little to zero lead on how to look at the problem. The period of having no crisp idea continued until I realized that the undetermined part of the one loop Pfaffian we left out in https://arxiv.org/abs/2204.02981 can be computed using topological string theory/new susy index https://arxiv.org/abs/2301.03602. The structure of the one-loop pfaffian was exactly the same as the structure of the one-loop coorrections to the EH action.
  
  Once I realized that string loop corrections to the EH action and the dilaton kinetic term can be computed using the new susy index, I think I got too excited, as I found a way to address the problem I wanted to solve for so long. Too strong excitement was poisonous to me, as I rushed to publish a paper without carefully checking factors of -1, 2, and pi. That resulted in unusually many revisions in these paper https://arxiv.org/abs/2302.12117 and https://arxiv.org/abs/2305.08263. I can make excuses if I want to, but at the end of the day all I can say is that I should've been much more careful, but I was blinded by my excitement. At this point, I don't think there is any more serious numerical error, but, who knows if I forgot to include a factor of 2 again! Since the question I am after concerns the exact numerical value of certain quantities, just the mere fact that the quantity is computable is not the end of the story. One should also get all the factors right. And it really sucks to get numerical factors wrong.
  
  One thing I worry is that probably some people might laugh at me after looking at my inspire or arxiv pages, and so many revisions. But, oh well, what can I do? I should do the best I can at any given moment. I just hope that this does not jeopardize my job prospect. My hope for getting a second postdoc or a faculty job in academia is not very high at this moment though.

• I am still glad that I had a gut to work on this problem alone, although I could've done a much better job.
  
  Despite the chaotic procedures, after seeing that the string one loop corrections can be in principle computed, it became much easier to convince people to collaborate with me on this problem. This will make my life easier and less scary, as having collaborators means that there can be more checks on numerical factors. So, I have a few follow ups on the results I mentioned above, which will hopefully lead to some good results.

• String field theory
  
  (When I came to  MIT, I had zero intention to work on string field theory, as I heard numerous times that it is extremely difficult to make progress in string field theory and get a job. Probably, I wouldn't have even started learning the topic if it wasn't for Harold's inputs and Ashoke's papers on D-instantons. But really, I came to accept that string field theory is a usable formalism thanks to Harold.)
  
  While I was able to find a way to compute some string loop corrections in the fluxless cases, the big question that remained was of course can one do such computations in non-trivial flux backgrounds as such backgrounds are where exciting things like moduli stabilization can happen. But, to do such computations, one needs a worlsheet description of flux compactifications, and it is well known that Ramond-Ramond backgrounds are extremely difficult to describe! I thought this was it, and no further progress can be made in a reasonable time scale.  Because of this, I think I felt quite stuck after this paper https://arxiv.org/abs/2305.08263.
  
  It could've been very difficult to think of using string field theory if it wasn't for some discussions  I had with Atakan.  I remember that during the discussions we talked about this paper https://arxiv.org/abs/1811.00032 at length. Although it was very exciting  that one can study Ramond-Ramond backgrounds perturbatively using string field theory,  at the moment, it wasn't very clear to me  how this result can be extended to flux compactifications because fluxes are quantized.
  
  Anyhow, once I remembered the discussions I decided to reach out to one of the authors, Minjae, And quite luckily for me, this led to a very productive collaboration that I am extremely happy about. It is not easy to find a very serious collaborator who's willing to work on a known to be difficult problem. This collaboration led to a nice result of finding background solution for GKP type flux vacua.
  
  This collaboration with Minjae  really convinced me that string field theory has a wide range of applicability. Now I have some hope that maybe it might be even possible to study de sitter quantum gravity with string field theory, at least perturbatively. I think I will keep working on string field theory for the near future. Probably I will have to also study more the foundational results in string field theory, most of which I don't fully appreciate yet.

• Cosmology.
  
  Recently, I attended a workshop on cosmology happened at Princeton. It was, intellectually, a very stimulating experience.
  
  Quite frequently, I thought about what the end game of the moduli stabilization program would be. If one finds a demonstrably well controlled vacuum, e.g., de Sitter, what would one do? Given that the main tools we use to analyze vacuum structure relies on the eft derived from string theory, it seemed very difficult to provide more than what a reasonable EFT can do.
  
  So despite that the questions of the existence of de Sitter vacua and scale separated vacua in string theory are interesting equations, I couldn't help but ask "so what?" Even if we do have such vacua, what will I do?  I did not have a very good answer. I still don't. But, the workshop at PCTS gave me some things to think about.
  
  The panel discussions and a talk by Daniel Baumann were very interesting.  Especially, I really like the visions that Juan Maldacena, Nima Arkani-Hamed, and Eva Silverstein layed  out. Of the problems, questions concerning understanding de Sitter quantum gravity seemed very important and interesting, e.g., entropy of de Sitter horizon, measure problem, and emergence of time, etc... This made me to think that I should really study the recent developements of gravitational path integral and it from qubit ideas. Nice thing about this subfield is also that many smart people are working on this topic, so it would be easier to find a person to bother.
  
  p.s) I saw a talk by Liam, during which he reported a very impressive progress made by the Cornell crew. They seemed to have found compactifications in which all the necessary ingredients to play with the KKLT idea are present, namely, compactifications with small w0, kahler moduli stabilization, and KS throats. The question of stability of anti-D3-brane susy breaking remains, but it appears to me that finding a well controlled vacuum is a problem of enlarging a search space of vacua and skillfully look for the corner where favorable statistics emerges.  So, in my opinion, the most pressing conceptual question is now answered by the Cornell group. The remaining problem is a technical one, albeit important.

• Jobs jobs jobs
  
  I finished most of the job applications. So, the long wait just began. I don't know if I will get any postdoc offer this application cycle, as I dug a deep hole for myself. (I mean I have been working on a very niche topic) But, at least I am happy that I had some fun during my first postdoc. 

Since I learned during my first postdoc that interacting with people with different backgrounds can be extremely helpful for my developments, I really hope that if I get a chance to do one more postdoc I will go to a place that is filled with people who don't work on the topic I work on.

I also applied for some faculty jobs this year. This is my first faculty job application. I don't have any idea how this thing will turn out. For one, I know that there are many excellent postdocs in high energy theory job market, who really deserve good positions. And also, nowadays, getting a faculty job right after the first postdoc seems very unusual unless the person is a superstar. So, I don't know how things will go, but at least I hope that even if I don't get any interviews or anything I will be able to get some feedbacks.

Nov 22, 2023

This is a continuation of the previous post. 

Deciding to stay in academia can be a comfortable choice. I get to do what I have been doing the past almost 8 years or more if I count the undergrad years. Comfortable choices are not always the best choices, but these are definitely easy choices in a sense. I wanted to generate some friction against making an easy decision, as I worried that it can lead to some sorts of regrets if I make decisions without being truly honest to myself. 

The regret can come from many directions. Also, I have many worries. After all this, it could just be that I might end up getting no postdoc offer. After three more years, it is highly likely that I won't get a faculty job at a place I like. So, I will eventually go to the industry. Then, I may regret that I lost earning potential and lost an opportunity to have a more comfortable life. Even after securing a faculty job, there is a chance that I won't get tenure, which could also mean that I will have to transition to industry after wasting O(10) years worth of earning potential. Also, personally, as an academic, quite likely I won't be living in a city/town that I really like. Academically, the community may not appreciate the research direction that I am hoping to undertake. And of course, I may not have a very lucrative career or research track record. Realistically, I shouldn't expect that I will make the most important progress. More realistic thing to expect is that, hopefully, I will keep making steady and gradual progress over time. So, it could be also very difficult to have the strong satisfactions by being an important figure who drives the progress. If things don't turn out quite the way I would like, maybe I will get stuck for good in the current research directions, and I will have to change what I do anyway. There are many reasons to be skeptical about the career in academia, or more narrowly in theoretical physics, most of which are avatars of the fear of uncertainty. (Although this song is about a slightly different context, I think the song "Million Reasons" by Lady Gaga encapsulates how I am feeling really well.)

But, realistically, whatever career I have, there will be always an element of uncertainty. Then what is it really, that is hiding under the uncertainty that makes me worried or stressed so much about staying in academia? 

I think, the answer is the fear of being not good enough at what I really want to be good at. I like physics. I like research. I want to be good at physics and research, and it will fill me with sorrow if I don't feel I am good enough. When doing research, it is not easy to get a validation. There are not so many ways to get validations or appreciations from the community. (This scarcity is also a reason why those validations are so precious.) A limited examples include acceptance to a journal, congrats or cheerful messages about results I have, awards, getting a position. It might be now clear where I am going with this. Internally, I think of promotions to next stages in my career as validations from the community that I am doing a good job and I am not just mediocre. If I cannot proceed to the next stage in my career, I will be very disappointed in myself, as I would quite likely take it as a sign that I am not good enough at what I like. And I don't want to go through this dreadful scenario. And the fear of being told that I am not good enough is the true source of fear, which manifests itself as the fear of uncertainty. An interesting thing is that this fear is born out of my deep care for physics. I wouldn't feel this fear, if I did not care about physics and research much.

In a way, even if I don't do physics, even if I don't do research, if I ever find what I am passionate about again, there is a good chance that I will start feeling the fear in the similar way. So assuming that I will know what I am thrilled about, probably, I will have to live with this fear. But, this may not be the worst life. If it becomes so clear that my passion cannot be equated with a sustainable career, I can try to find something else to focus on. Until then, I can try to enjoy as much as I can. To be quite frank, having nothing to be passionate about is much worse than fearing about being bad at what I love. When I first started studying physics and mathematics, I was really really bad at them, as I have always been a slow learner. But, having what I like and what I want to be good at, despite the fact that I sucked at them, was a source of a delight that made my early life quite enjoyable despite my somewhat unfortunate childhood. And what fun is life, if there are no ups and downs? Life will be quite boring, if everything works out as planned.

So here comes my one good reason to stay. The stress, anxiety, worry, and many negative emotions I feel about staying in academia are rooted in the fact that I deeply care about research in physics. And, it won't be wise to walk away from something I really love because I care too much about that something unless I come to accept that I am not good enough to have a sustainable career in physics anymore. The better thing to do for me seems to learn how to deal with the anxiety. (I would still appreciate if I can earn more. For one dumb reason, I love spending money on food and there is no limit to it. But the finance is not a very important deciding factor at this point. But who knows how my thoughts will change in the future! However, this will be a problem for the future.)

July 27, 2023

Soon, it will be again a job application season for me, meaning that I will have to decide if I want to apply for postdocs (and a few faculties positions maybe) or go to the industry.

If things are quite ideal, I wouldn't even have a second thought about staying in academia. I enjoy the immense freedom to do whatever I want to do, and quite frankly stimulating intellectual interactions with my colleagues is something I cannot easily let go. But, ideal situations are called ideal, because such situations only live in my wildest imagination. 

There are scientific and sociological reasons that make academia not quite ideal for me at least. But, although it may sound like an excuse, I would argue that knowing what makes the situation not ideal is a step forward, as we can better the situations if we know what is troubling. The scientific reasons I have cannot be completely disentangled from the sociological reasons. Let me start without separating those two reasons very clearly.

Perhaps in a controversial way, I am a string theorist who still believes and thinks that for a physical theory to be a scientific theory, the theory in question should be testable via experiments, observations, or any similar forms. In fact, one of the strongest motivations for me to start studying string theory was I wanted to see myself if string theory as many people around me, when I was younger, claimed is really a theory that is not even wrong. I wasn't drawn into string theory because of fancy mathematics, or esoteric topics connected to string theory. But, because of potentially the most mundane and boring question "can string theory be a theory of our universe?"

The very prerequisite to making predictions or postdictions is to first reproduce all the things that we already observed. In my opinion, this is the very minimum requirement that any theory should pass that dares to be called a physical theory.

In the context of string theory, this will mean that at the very least, we should have a (meta) stable vacuum that at low energy does not have supersymmetry, and has SM and positive CC. Well, it does not really have to be a meta stable vacuum, but really the important thing is that the "solution" in question should look like a meta stable vacuum. 

To find such (meta) stable vacua, what do we need to know? In my opinion, there are two important problems we need to solve or further our understanding of. 

1. Can one precisely and accurately compute properties of string compactifications, brane worlds, or whatever scenarios or constructions you like?

2. Can one find mechanisms or algorithms to help us search for special vacua that might look like our universe?

Those two problems are intertwined obviously. To figure out mechanisms to find interesting vacua, we need to know what we are playing with. To compute anything in string theory, we need a vacuum to perturb around. Those two problems cannot be easily separated. 

Now here comes my frustrations. I will not attempt to sugarcoat the situation. It is commonly believed that, at least from the conversations I have had with many of my colleagues this is the impression I had,  these two problems are very difficult to make progress on. Maybe they are right, or maybe they are wrong. But somehow, I cannot stop thinking this has a flavor of a self fulfilling prophecy. Prominent figures, established researchers and senior researchers who have spent years to study string theory in the early days keep repeating the ideas that these are difficult problems with no practical way forward oftentimes, and younger generations who don't have sufficient academic maturity to judge themselves listen to more experienced researchers to internalize the ideas that these are indeed very difficult problems. Therefore, less and less people entering the field are thinking about these important, in my opinion, problems. The problem is that if less and less people are working on a big problem that problem will feel much more difficult eventually as there are less ideas, less approaches, less computations being done, and therefore slower progress that are enough to give people impressions that indeed the problems are difficult. And maybe for this reason, less and less young people are entering the field with the goal to connect string theory to the real world. 

I am a person who can be easily fooled by my irrational optimisms. But, nevertheless, I believe or want to believe that there should be a practical way forwards although we may not know them yet. And this is why, as long as I stay in this field, I want to work on those problems although I maybe not the right person to go after these problems. But I acknowledge that there are to the large extent glaring uncertainties. When, and how will we figure out such ways? Although I believe that struggling through uncertainties is something we researchers just accept and live with it, it may not be a very attractive thing for some people. And even for me, I hate to deal with this uncertainty, although I will have to just suck it up. But, suppose I continue my work in academia. Certainly, I cannot keep working alone for it is difficult both scientifically and personally. And, if I am lucky and successful enough to become a faculty at a research institution, an ideal situation would be for me to work with students and postdocs who are motivated. But, will it be an easy way forward? 

I have many thoughts and worries about this aspect of a future life say. For one, in this competitive job market situation I am not sure if I can be lucky enough to secure a faculty position at a research institution where I am supported to do good research. One can say I am being too pessimistic and I should stay more positive. But, I have a few real reasons. Essentially, I am working on niche topics, that many people already moved away from. If a university is to invest in me to hire me as a faculty, certainly a university will want to make sure that what I work on can turn into something meaningful, something good, or something that can excite people before it is too late. Although I believe that the research direction I am following is very important for string theory's sake, I don't know how many non-string theorists will agree that spending years and years to try to connect string theory to the real world is something they should invest in. It is a risky investment, like a venture investment! (although string theory is too old to be called a venture) And quite frankly, even I am not certain how long of a time will take for us string theorists to confidently claim that "behold! we have a vacuum that looks like our universe up to the experimental precision!" Then, why do universities need to invest in me for this venture is risky and it is uncertain when the institution will get their dividends?

But, let's not be too pessimistic and let's allow myself to have a happy thought. In this imagination, I found myself a faculty position at a good research university (I am not asking for places like Princeton, Harvard, Stanford, etc.. even in my wildest imagination) and I am reasonably well supported to do research. Say, I teach a class every semester, and I have just enough funding to have 1 or 2 students, and sometimes if I am lucky I have a shared postdoc with hopefully other faculties working on theoretical physics. I want to keep working on these difficult problems, as I have no sense of self preservation in a sense. But, will my students and postdocs also want to dive into this risky business? If I am extremely lucky, I may find some collaborators, students, postdocs who are motivated to work on those difficult problems. But, I shouldn't ask my life to be so perfect for me and I need to embrace and prepare for the worse scenarios in which I will have to work most of the time alone, if I am too stubborn to work on what I think is important and interesting. Now the real worry is, will I get to produce good results? I am a person who can easily fool myself, and I am certainly not a genius. If I cannot get constant feedbacks, at certain points, if I become a crack pot of sort, who will and can stop me for I am being extremely stubborn? And even if I don't fall to the dark side, and keep producing results, I am just one person. As a single person, who is quite ordinary, can I make a big breakthrough to make a big change? I am not sure.

So, in summary, I am having various thoughts about my career and my life at a very interesting time. The time which having doubts and too many thoughts is not the best, as the clock is ticking and the application season is near. But, maybe it is the right time to think about this problem. If I go on to the second postdoc, and possibly to faculty positions assuming I get lucky, I will devote many many years of my life into string theory or theoretical physics more broadly. This is a big commitment. And, it is better to make a big commitment after having serious thoughts.

June 23, 2023