2024

It is already the end of the year again. 

I haven't worked as much as I wanted and produced somewhat little compared to previous years. But, at least, I spent more time on how to spend my time and what to do. And after a short trip to London, I caught a mild flu that came with a mild fever. There is no better time to philosophize than when I am delusional under the influence of the fever. Also, I heard from Imperial College London that I am shortlisted for the faculty position. This exciting news gave me a little panic attack. For two reasons: the thought of becoming a faculty and an advisor to students made me feel the weight of immense responsibility, and I usually get extremely nervous during an interview. So it is good to clear the thoughts as well.

Of those thoughts, perhaps the most urgent one for me is to have an answer to the lingering problem that keeps popping up in my head is why I do theoretical physics. I have to admit that I don't do theoretical physics for fun or joy, for most of the time, working on theoretical physics is quite stressful and oftentimes painful. I have the audacity to admit that I do theoretical physics to have a chance at doing something great that will be meaningful even if I don't see the light in my lifetime. You know, there is a saying in Korea that tigers leave their fur, whereas people leave their names. As I am quite an ordinary person, making such an impact won't likely happen, but I hope that if I work hard, the probability will not be zero.

Asking the right questions in the right context at the right moment in spacetime is much more impactful than answering questions that have already been asked and looked at a million times. Unfortunately, the questions I can ask at this point are formed and affected by what I hear, read, and study. Probably, my limited linguistic capabilities also limit how I think. To be quite frank, the questions I can ask inevitably are already asked by many people before me. Until I can come up with really an original question that is right in many ways, maybe what I can do at the moment is keep thinking and deciding what the right questions are. 

As I am a person who is relatively well led by my personal frustration, I will choose my frustration as a guiding principle. I like to work on and think about things that make me feel frustrated, overwhelmed, and stuck in the right way.

What are the profound claims and problems in modern physics I don't really like or rather I despise? I can easily say two cases:

1. The anthropic principle

2. Naive attempts to solve the cosmological measure problem

What are the profound subjects that I am rather disappointed in? 

1. Any attempts to formulate quantum gravity via some sort of scattering of gravitons.

2. Relatedly, the holographic principle.

I will explain why I am not happy about those. For me, the intellectual utility of science lies in its ability to form and progressively answer the question about why? Of course, science so far has never given the complete answer to why-type questions, but asking why has always been fruitful. For example, one can ask why magnets attract each other. In an attempt to answer why, one may come up with magnetic fields and forces that explain how magnets attract each other. In an attempt to understand why magnetic fields are generated, one can understand how magnetic moments source magnetic fields, etc.. My resentment towards the anthropic principle and all the attempts I know that try to address the cosmological measure problem either seem to give up on asking why or tell me that I should stop asking why. If an answer to the question of why are we here the way we are here is because this is the only universe we can be here, whose validity is subject to our prejudice on how minds form, I cannot really accept the answer. Similarly, all of the solutions to the measure problem require making up rules that are based on heavily questionable motivations.  

What I really want is a theory capable of describing dynamical and quantum changes in spacetime, whatever that is. Crucially, to understand the measure problem and relatedly physical cosmology, the theory in question should be able to describe a transition between vastly different spacetimes so that it can give us a tool to describe how the universe selects out a universe like ours, which naively should be extremely difficult to be selected out of infinitely many possible solutions. Quite likely, to be able to describe such transitions, we need a theory that knows about not only the "on-shell" physics but also the "off-shell" physics. Quite obviously, this leads to my disappointment in attempts to define quantum gravity via scattering and the holographic principle. Well, in fact, the scattering approach is more troublesome, as it has a very hard time describing the condensation of gravitons that induces the change of spacetime. 

Without any doubt, to completely ease the frustration I feel, we may need multiple decades of time. Or, maybe it could well be that the human species is too inferior to comprehend the theory.  Nevertheless, it is fun to think about how to make infinitesimal progress in light of the massive problem we are facing.  

1. The way we organize theory is greatly assisted by symmetry. One can argue that the reason why we do not have a good idea about how to formulate non-perturbative quantum gravity is that we do not know much about what the full symmetry structure must be. A reasonable hope is to, therefore, have a better understanding of the symmetry structure of quantum gravity and use it to constrain the form of the theory.
   
   In the context of the BRST quantization of string theory, we have a very limited understanding of the symmetry structure. This is because despite that we know that the symmetry is governed by something called L-infinity and A-infinity, this symmetry structure is only capable of describing infinitesimal gauge symmetry. To really understand the full gauge symmetry, we need to move away from the infinitesimal ones.
   
   I don't think it would be particularly fruitful to guess in the wilderness what the gauge symmetry structure is. But, maybe we are not in the complete dark as we have some controlled examples, such as mirror dual of Kodaira-Spencer theory that should be capable of describing spacetime change, e.g., from the Landau-Ginzburg to a large volume Calabi-Yau. How can we translate the symmetry structure into something known or can be posed in math. The other fruitful direction may be to understand the tachyon condensation non-perturbatively in closed string. The hope is that once we can understand the non-perturbative change of spacetime in string theory, we might have a better understanding of the symmetry.   

2. To understand the measure problem, we need to first understand the admissible set of spacetimes. A much more mundane question will be to understand the admissible (static) cosmological saddle points in string theory that will provide an approximate basis for the inquiries in the measure problem. For this, unfortunately, I should be again a broken record and say that one needs to understand the landscape and the swampland of string theory rather precisely.

So, what do I want to do in the next year, and hopefully many more years to come? (I really hope that I will get some faculty jobs. I realized my obsession towards physics is much bigger than what I thought. If I can get the Imperial one, I would be very happy, but the position seems to be very competitive.)

Well, I have one trivial answer for the immediate future. I will develop tools to compute alpha' and g_s corrections to understand the validity of cosmological solutions in weakly coupled type II string theories. Currently, the worst offender of the problems appears to be the susy breaking in the context of KPV. I hope that with a reasonable effort ranging from a year to two, we may have a very clear understanding of the stability issue of KPV. My worry is that it might be very difficult to have a very well-controlled clean example of a cosmological solution in weakly coupled type IIB due to the limited tadpole. If this turns out to be the case, one should start seeking cosmological solutions in genuine F-theory, which might take O(10) years which will turn the enterprise into a long-term investigation.

Beyond this trivial answer, I don't exactly know where I will go. But, at least, I want to get back to topological string theory, this time with a focus on the string field-theoretic nature. I am really hoping to learn more about the symmetry structure of the theory.   Also, maybe it is a good time for me to seriously think about the measure problem on my own. I have been an external observer to the discussion, as I personally felt I had nothing useful to add. But, if I don't do anything, I will never be able to add anything useful to the discourse. So I rather start by doing something very dumb and redundant, with the hope that I will produce useful results on my own before it is too late.

Dec 24, 2024

It has been a few months since I moved to Bay area to work at Stanford. The move was hectic as expected, but it was done. The bay area is beautiful, although the cost of living is probably too high for me. I don't like that I have to rely on car/driving to get anything done basically, but at the same time, I appreciate access to fresher seafood, better grocery options, and beautiful local hiking trails. I have been hiking almost every weekend, and even with this rate, I am not sure if I can explore all the places I saved on AllTrails app! 

Science-wise, the spectrum of physics that people do at SITP is quite different from what I am used to. So, in many ways, it has been quite refreshing, although I find it hard to follow discussions most of the time. Hopefully, I will pick up some keywords soon, so that I can contribute to the discussions in meaningful ways. Of the topics discussed intensely at SITP, I think the following topics are especially interesting to me

1. BFSS

2. Hyperbolic geometry

3. Chaos

As I am a very slow person, I am not sure if I would be able to learn enough to work on any of them during my time here, but having some good ideas about what are interesting problems in such categories is hopefully achievable.

At the same time, I feel, to a marginal degree, some academic isolation in that it is hard to find local people to have discussions about the problems I find interesting. Given that what I decided to do is quite a niche topic everywhere in the world, this is partly on me, and I am extremely grateful to the institution for hiring me despite my unusual taste in research. 

Before coming to Stanford, I seriously thought about changing my research direction somewhat significantly. This thought was motivated by some of my frustrations, both scientific and sociological. But, eventually, I just decided to go even further than developing the original research program, and do what nobody in my current community appears to be wanting to do. 

It can be out of my arrogance, if there is any left in me, or my belief that most of the people are not willing to work on necessary things that are not considered glamorous. Yes, I sound like an old man who complains about the younger generation. I think the kind of problems I consider extremely important, e.g., developing string perturbation theory (and hopefully beyond ) in more generic backgrounds and computing things in such backgrounds, precisely fall into that category. The problems that "someone should work on, but I don't want to." Of course, there are more problems that I consider extremely important. But among these, I think this one stands out as I see a practical way forward. 

Because I believe that if to the community that such problems are shown to be not so intractably difficult, more people will work on them eventually, and considering I might not have enough time to work on every interesting problem I can think of in academia (this Stanford postdoc will be my last postdoc), I thought, perhaps the good I can do will be to do something that some other people might pick up later. So my hope is that I can do as much as I can do to set up systematics, even some programs that other researchers can use, to do computations and work that I want to do if I have more time in the field. My most recent paper was to show that, and because of the motivation, I made my paper somewhat too verbose to include all the details. 

Fortunately, some students at SITP showed interest in my research program. Hope that I will get to do something with them. Oh, and forgot to mention, I found a few new collaborators to work on few of the niche problems I wanted to solve. Frankly, I am very happy about this.

And, the application season came back already. As a person who consistently makes a bad life decision, I decided to apply to only a handful (literally!) of places for faculty jobs. I have a good set of arguments to defend my decision although it can be an excuse to let my career as an academic slowly die. But, I have less obsession to stay and get a faculty job. There is more to life than physics and work. And I am a luxury goods that not all universities can afford. (This is a joke, you can laugh)

Happy New Year!

The new year just started, and I am off to this new year with a few thoughts. 

1. Job market and applications
   
   As is quite evident from my posts, for the last few weeks, my brain was pretty much occupied by my applications. To some degree, I am still thinking about the applications and the job market situations, but the frequency and the intensity have decreased by a lot.
   
   As I went on to the job market for this application cycle, I knew that I will have a difficult time finding a position for a several reasons. To name a few, places at which string compactification/pheno activities are vibrant are rare, I have been working on niche topics, and on top of that the topics I worked on mostly (moduli stabilization) to some may seem controversial and many people have strong opinions, maybe too strong one can say, about this topic. Furthermore, I started spending significant time on string field theory. So I thought I would be lucky to be offered even a single job. Despite all those reasons, I was still hoping to have not so difficult time. But, usually bad feelings are right.
   
   When I lost most of my hope, I heard pleasant surprise from University X. I cannot express my gratitude for offering me a postdoc, faculties there were very kind to express genuine interest in the line of work I do despite I do things quite different from what people at University X do. It feels good to be acknowledged by someone. I think I really needed it. I will remember this gratitude for a very long time.
   
   I think the long wait is still there though. But, now with much less stress. I am really hoping that I will get at least one faculty interview request from somewhere.
   
   On the other hand, I think how the offers from best places are made shows what types of and styles of research are appreciated by senior faculties and the community.  I have been looking at the rumor mill somewhat closely to get the grip of which research directions and styles are appreciated. As the deadline for accepting offer can be as late as Feb 15th, making a conclusion at this point is too hasty. But, it still gives me good food for thought.
   
   There are a few things I learned this cycle, of those one thing I want to try is to learn how to come up with simple and solvable toy models that might teach me about some big problems that are too difficult to directly solve.  As I haven't done this type of study, it may take a while for me to really get up to speed , but I think it would be worthwhile to try.  I think it is in general a very good idea to start with a problem I want to solve, and remove all the unnecessary details until I am left with the simple gist of the problem, which will give me a clearer picture. And after all, this is how to make fundamental insights I gather. I should've spent more effort on doing this.

2. I am thinking about what I want to do in the coming year.
   
   A. I think I will continue developing tools to compute various one-loop amplitudes in string orientifold compactifications, eventually with RR fluxes of course. I started out this as I wanted to solidify the supersymmetric AdS vacua with small c.c. me and my collaborators found in https://arxiv.org/abs/2107.09064 by showing that these solutions are well controlled. We made some estimates and arguments on why we judged the solutions to be well controlled in the paper, but arguments are fuzzy and cannot be crystal clear. And, since, some experts think that something must go wrong in our solutions in light of some swampland conjectures,  I thought it would be very important to tighten perhaps the only loose ends in our solutions to convince the community: namely, string loop corrections to the Kahler potential and the numerical values of one-loop pfaffian of the non-perturbative superpotential.
   
   I personally think irrespective of the swampland vs landscape debate, this problem is important in its own right although it is not a zero-th order problem. It is kind of a mopping operation that someone has to do. As this problem is too dirty, and it takes long time to make progress, it is not a very attractive problem for many people. So, even though I think this is an important problem,  I think I will have to keep working on this semi-alone until I finally compute things at least at one-loop very explicitly.
   
   I think it is possible to get there, but the problems are
   a. It will probably take a very long time to get to the end point.
   b. Probably, I wouldn't get much recognitions by doing it.  Because of the nature of the problem, and due to the fact that people have strong opinions on KKLT let's say.
   c. And most importantly, I don't like to engage in debates for too long. It wears me out.
   So, probably, building tools to better understand the effective action of string compactification will not be a self-sustainable way to earn bucks to pay bills.
   
   B.  In the past year, I found quite a few recent developments that made me very excited. In random order, I found the following developments very exciting
   
   https://arxiv.org/abs/2312.05303
   https://arxiv.org/abs/2310.02490
   https://arxiv.org/abs/2312.12592
   https://arxiv.org/abs/2312.15111
   https://arxiv.org/abs/2208.14233
   https://arxiv.org/abs/2306.00940
   https://arxiv.org/abs/2104.13380
   https://arxiv.org/abs/2311.09334
   
   I don't think I will write here why I was so excited by the above mentioned papers, as I could write something wrong at this point. I think I will spend significant time to study the above papers to see if there is anything I can add. I learn things slow, but hopefully I will catch up soon.
   
   C. I think I will keep spending time on string field theory. Working on string field theory may not be the best idea in terms of job prospects, but I think there are some fundamental questions that are left unanswered. I want to know if those problems are solvable in a humane time scale. Until I get the sense of the time scale, I will have to work on some small problems with the intention to approach that goal.
   
   D. I should also probably learn how to properly code and study statistics?  
   
   

3. It really saddens me in a way that quite likely this year will be my last year in Boston and I will have to leave Boston soon. I really love the city, and I think this is the city I like the most in all of the places in the US.  

Jan 1, 2024