All of libai's Comments + Replies

libai10

To be fair, almost nobody considered a pandemic to be a serious possibility prior to 2020, so it is understandable that pandemic preparedness research was a low-priority area. There may be lots of open and answerable questions in unpopular topics, but if the topic is obscure, the payoff for making a discovery is small (in terms of reputation and recognition).

Of course, COVID-19 has proven to us that pandemic research is important, and immediately researchers poured in from everywhere to work on various facets of the problem (e.g., I even joined in an effor... (read more)

5ChristianKl
In the US alone depending on the year there are something between 10,000 and 60,000 flu deaths and a lot of additional harm due to people being ill. Whether or not pandemics are a concern it's an important problem to deal with that.  There was money in pandemic preparedness. The Gates Foundation and organizations like CEPI were interested in it. They let themselves be conned by mRNA researchers and as a result funded mRNA research where there's a good chance that it had net harm as it made us focus our vaccine trials on mRNA vaccines instead of focusing them on well-understand existing vaccine platforms that are easy to scale up and come with less side-effects.  The study from 2018 I referred is written in a way it is to advocate that part of this money goes into studying ivermectin for influenza. With the knowledge of hindsight that would have been more important. In any case, my main point here is that what was prioritized (or was found to be valuable in Larry McEnerney terms) and what was important were two different things.  If you want to do important research and not just research that's prioritized (found to be valuable by a particular community) it's important to be able to mentally distinguish the two. Paradigm changing research for example generally isn't valuable for the community that operates in an existing paradigm. Sydney Brenner who was for example on of the people who started the molecular biology field is on record for saying that the kind of paradigm creating work back then would have been a hard time getting funded in today's enviroment.  Given that there's an efficient market as far as producing work that's valued by established funders and not an efficient market for creating important work any researcher that actually wants to do important work and not just work that's perceived as valuable has to keep the two apart. The efficient market hypothesis implies that most of the open opportunities to do important work are not seen as valuable
libai10

Yeah, I agree that the EMH holds true more for incremental research than for truly groundbreaking ideas. I'm not too familiar with MCMC or Bayesian inference so correct me if I'm wrong, but I'm guessing these advancements required combining of ideas that nobody expected would work? The deep learning revolution could probably have happened sooner (in the sense that all the prerequisite tools existed), but few people before 2010 expected neural networks to work so consequently the inefficiencies there remained undiscovered.

At the same time, I wouldn't denigr... (read more)

3ChristianKl
I think the problem with MCMC is that's an incredible dirty thing from the perspective of a mathematician. It's way to practically useful as opposed to being about mathematical theorems. MCMC is about doing an efficient way to do calculation and doing calculations is low status for mathematicians. It has ugly randomness in it. I was personally taught MCMC when studying bioinformatics and I was a bit surprised when talking with a friend who was a math Phd who had a problem where MCMC would have worked very well for a subproblem but it was completely out his radar.  MCMC was something that came out of compuer science and not out of the statistic community. Most people in statistics cared about statistical significance. The math community already looks down at the statistics community and MCMC seems to be even worse from that perspective. My statistics proof said that in principle bioinformatics could have had been a subfield of statistics but the way of doing things was in the beginning rejected by the statistics community so that bioinformatics had to become it's own field (and it's the field where MCMC was used a lot because you actually need it for the problems that bioinformatics cares about). 
3Radford Neal
Certainly some incremental research is very useful.  But much of it isn't.  I'm not familiar with the ACL and EMNLP conferences, but for ML and statistics, there are large numbers of papers that don't really contribute much (and these aren't failed attempts at breakthroughs).  You can see that this must be true from the sheer volume of papers now - there can't possibly be that many actual advances. For LDPC codes, it certainly was true that for years people didn't realize their potential.  But there wasn't any good reason not to investigate - it's sort of like nobody pointing a telescope at Saturn because Venus turned out to be rather featureless, and why would Saturn be different?  There was a bit of tunnel vision, with an unjustified belief that one couldn't really expect much more than what the codes being investigated delivered - though one could of course publish lots of papers on a new variation in sequential decoding of convolutional codes. (There was good evidence that this would never lead to the Shannon limit - but that of course must surely be unobtainable...) Regarding MCMC and Bayesian inference, I think there was just nobody making the connection - nobody who actually knew what the methods from physics could do, and also knew what the computational obstacles for Bayesian inference were.  I don't think anyone thought of applying the Metropolis algorithm to Bayesian inference and then said, "but surely that wouldn't work...".  It's obviously worth a try.
libai10

True, I guess a more precise statement is "most problems that are important and solvable are already solved". There are lots of small gaps in my research as well, like "what if we make a minor adjustment to method X" -- whatever the outcome, it's below the bar for a publication so they're generally left untouched.

7ChristianKl
No, there are plenty of important problems that nobody has an incentive to solve. See Eliezer's Inadequate Equilibria. It's central that there's a research community that cares about the problem. Take Ivermectin pre-COVID. It worked very well for getting rid of parasites after being invented in 1975. Well enough to lead to a Nobel prize. In 2018 there's a paper saying: The question whether Ivermectin is a viable treatment against influenza and maybe a broad spectrum antiviral is an important problem. On the other hand it's not a very valuable problem for anyone to find out given that Ivermectin is long off patent.  The way the last sentence of the paper is formulate is very interesting. As far as Influenza being important, the fact that we have every year a lot of influenza deaths should be enough to demonstrate that it's an important problem. The community that produces regular drugs however doesn't really care about repurposing a generic.  On the other hand there's a community that cares for pandemic preparedness. The pandemic preparedness community cares less about whether it's possible to patent treatments and cares more about health outcomes so he pitches it as being valuable for the pandemic preparedness community.  The tools to solve the problem of whether or not you can use ivermectin as antiviral against influenza and also against Coronaviruses exist since it hit the market in 1981. It was just never valuable enough for anybody to find out until some people thought about running small trials for all the substances that might help against COVID-19. The people who did consider it valuable also were mostly small funders so we still haven't highly powered trials that tell us with high certainty about the effects of ivermectin. The big healthcare funders didn't consider it valuable to fund the studies early in the pandemic but that doesn't mean running the studies wasn't important. MIRI's attempt to publish ideas into the academic community had the proble