Might you be able to slightly retrain so as to become an expert on medium-term and long-term biosecurity risks? Biological engineering presents serious GCR risk over the next 50 years (and of course after that, as well), and very few people are trying to think through the issues on more than a 10-year time horizon. FHI, CSER, GiveWell, and perhaps others each have a decent chance of wanting to hire people into such research positions over the next few years. (GiveWell is looking to hire a biosecurity program manager right now, but I assume you can't acquire the requisite training and background immediately.)
This is the kind of 'I-wouldn't-have-thought-of-that' answer I was hoping for.
It would require substantial retraining, but this seems like a direction I could move in by choosing the appropriate post-doc, while also doing some useful work along the way. The general class of 'using biology to ensure the future occurs' contains a lot of potentially interesting things like plant biology and research involving things like salt and pathogen tolerant crops. Looks like I have some research to do :)
Did you, by any chance, read Andre Almeida on trehalose and desiccation/salt/cold tolerance in plants? (Not that that's particularly interesting, but my impression was that it was 'solid'.) (Also, sometimes people develop salt-tolerant wheat in vitro without any research as to how its symbionts in vivo influence its performance, which should impact study reproducibility.)
The problem with being interested in biosecurity risks is that the books about witches are written by wizards, who get strange ideas around five in the morning... And it would require a synthesis of giant amounts of current research which [for a layman] looks very patchy and inconsistent; it wouldn't probably be a fulfilling occupation. Although of course this is otherwise a great idea. Perhaps if the person concentrated on a specific area, like crops or biofuels?
Research (that I've seen) is in general patchy and inconsistent. But I take your point, it might be a frustrating enterprise. I think concentrating on a specific area is almost certainly a good idea.
Some relevant questions that come to my mind:
My overall impression is that you seem like the kind of person whos happiness is largely tied to how big an impact you have, and who is rather altruistic. And so it seems important for you to find something that enables you to have a big impact. You also seem young enough where it seems worth thinking about the long-run. It seems worth taking the time to do a lot of research and make the right decision.
Most Americans spend too little time on higher-level actions, like being strategic - doing a quick analysis of what your goals are, and which Level 1 or Level 2 actions would best accomplish those goals. Witness the hordes of lawyers who spend thirty years on the Level 1 action of working at a law firm, three years on the Level 2 action of getting a law degree, and three minutes on the Level 3 action of deciding what to do after college.
Yes. I'm rather annoyed at myself for only now giving level 3 the kind of attention it deserves. Level 3 is hard though. Largely because other people can't help you as much. I'm kind of agnostic about what I want, to be honest. Nor do I have good information about my comparative advantages (due to relative ignorance of other fields) and the magnitudes of the trade offs to be made. Now is a time when I can take the time to think on and research these questions.
I'd estimate my altruism fluctuates between zero and ~70% on a daily basis, with a peak in the mornings immediately after get caffeinated.
Yes. I'm rather annoyed at myself for only now giving level 3 the kind of attention it deserves.
You're fortunate - that's the sound rationalists make when they level up :)
To what extent do you want to be happy?
Just a thought, this may be an instrumental value in addition to a terminal one. Moreover, it may be worth holding mentally as a terminal value, and only highlighting its instrumentality when it clashes with other terminal values.
Norman Borlaug is the poster child of how to use genetic manipulation for large-scale impact as an individual, so I don't think your degree is pointed in the wrong direction. But it is the nature of established institutions to fail at revolutionary thinking, so a survey of the 'heavyweights' in your field will tend to be disappointing.
I think a large part of my lack of enthusiasm comes from my belief that advances in artificial intelligence are going to make human-run biology irrelevant before long.
We have only crappy guesses about the completion date for the AGI project, and the success of FAI in particular is contingent on how well our civilization runs in the interim. For example, wartime research might involve risky choices in AGI development, because they have a more urgent need for rapid deployment- an arms race for the 'first' AGI would be terrible for our chances of FAI. Genomics won't help us build a mind, but it can help foster an environment where that research is more likely to go well (see Borlaug again). You might, say, investigate the regulatory networks surrounding genes correlated with sociability or IQ.
I think the ultimate problems we're tackling (predicting genotype from phenotype, reliable manipulation of biology, curing cancer/aging/death) are insoluble with our current methods - we need effective robots to do the experiments, and A.I. to interpret the results.
Do you believe that you can reliably distinguish 'problems that cannot be solved by humans' from 'problems that humans could solve in principle but haven't yet'? Personally, I'm very bad at this, especially when the solutions involve unexpected lateral thinking. While I do agree that AGI is more or less the last human invention, I doubt that it's the next one- we haven't run out of other things to invent, and I'd be surprised if that was the case in the narrower area of genomics.
It's probably worth pointing out that you are at the exact stage in your PhD that is most known for general burnout. This looks suspiciously like such an event, with an atypical LW filter. So, this: "I think a large part of my lack of enthusiasm comes from my belief that advances in artificial intelligence..." is likely to be false, since many of your colleagues are experiencing similar feelings at a similar time.
Do you believe that you can reliably distinguish 'problems that cannot be solved by humans' from 'problems that humans could solve in principle but haven't yet'?
"Solvable in principle by humans" and "solvable by humans with our current methods" are not the same thing. Most of the fruits that you can gather with the current tools of molecular biology seem to be picked. There are also a lot of man-hours thrown on them.
Progress in biology will come more from developing new methods than using the existing methods.
Most of the fruits that you can gather with the current tools of molecular biology seem to be picked.
I am not quite sure what the scope of the statement is, but that's strongly counter to the things I'm hearing from the molecular biologists that I know (two family members and a few close friends- I'm plugged in to the field, but not a member of it). Could you elaborate on your reasons for this belief?
My impression is that the discipline has spent the last couple decades amassing a huge (huge) database of observed genes and proteins and whatnot, and isn't even close to slowing down. The problem is in navigating that wealth of observation and translating it in to actionable technologies. New methods will make discovery radically more efficient, but the technologically available space that these scientists have yet to explore is so large as to be intimidating. If anything, the molecular biologists I know are discouraged by the size of the problem being solved relative to the number of people working on it- they feel like their best efforts can only chip away at an incredibly large edifice.
If anything, the molecular biologists I know are discouraged by the size of the problem being solved relative to the number of people working on it-
The main question is the value of a marginal molecular biologist chipping away at the problems with current methods.
All those new knowledge about genes we got through the human genome project produces few promising leads for new drugs. Big Pharma companies sit on large pile of cash at a time where the interest rates are near zero and they buy back shares while laying off scientists.
Currently we don't know what 1/4 to 1/3 of the human genes do. Those where we do know a function might have additional functions. With a lot of hard work we might find out more functions, but that doesn't bring us much further. Few get a few new drug targets but drug targets aren't the limiting factor for drug discovery. Predicting which drugs actually help is the more important issues as clinical trials are really expensive. Most drugs put into clinical trials fail.
Apart from the actual use of the science, progress is hold back by poor ability to replicate findings. Some of that is because scientists don't work properly but it can also be that the monoclonal antibody you order today is not the same as the one that you ordered a month ago even through you ordered it from the same lab and it has the same label.
Then even if your finding is correct and you publish it, that doesn't mean that your paper is going to be read. The language in which papers are written is very complicated and not easily interpretable by computers.
This all hits the nail on the head I think. The marginal value of my PhD is, I'm convinced, at most zero, and perhaps negative, because it adds to the noise. The replicability of papers is significantly hindered by lack of automation, to my mind.
Also, saying that we don't know what 1/4 to 1/3 of human genes do is wildly optimistic. Better to say we have some idea what 2/3 of them do.
I don't mean to come across as super optimistic with respect to strong A.I., or even A.I. in general. I should have written '50 years give or take 50'. It's just that i think my field's progress rate is determined by the inflow of methods from other fields, and that the current problems it faces are insoluble using current ones. I think people who aren't immersed in the field get a mistaken impression about this because papers and press releases must communicate an artificial sense of progress and certainty to succeed. Word in the trenches is that we're mired in an intractable mess of unknowns.
As an example - take Aubrey de Grey's SENS program. He lays out all these alterations he thinks he can make to fix the problem of aging. But he seems to think of biology as modular and easily mutable. A biologist expects each individual step he proposes to face dozens of unforeseen problems, and to have many, many unpredictable knock-on effects, over a wide range of detectability and severity. Dealing with them all isn't doable right now, while single grad students take 5 year to determine a few of each genes many interactions and functions.
As for burnout - I'd agree with you if this was a recent development. But I've felt this way for years. It's just that now action is required. It's possible I've been burnt out for years. This has been suggested to me - my working environment is exceptionally poor - which is something I can say semi-objectively due to the number of people who have quit and/or echoed my feelings on the matter. I'm trying not to let those feelings influence me too much however.
I don't see artificial intelligence improving in a way that suggest that it soon solves all our biological problems.
As far as effective robots go, you could call high-throughput sequencing machines effective robots. Cheaper gene sequencing then produced a lot of new knowledge. Fortunately databases like uniprot allow access towards the produced knowledge that goes well beyond what scientific papers can provide. Imagine the mess if all the information about genetic sequences would be written in papers and textbooks.
We could have further success in biology if we manage to treat other biological problems the same we. Instead of focusing on insight, we focus on building better tools and infrastructure to organize the resulting knowledge in a useful fashion.
With smart watches that integrate constant heart rate monitoring, we have suddenly a lot of data but are still lacking in interpretation. Lack of use cases for data currently stalls development (see Apple). It might be possible to develop early warning signals for the illnesses like the flu with pick up signals before the patient is consciously aware of the flu.
Obesity is also an interesting subject. To me BMI feels like a stone age diagnostic tool. There's no way that the statistic is optimal but it still get's used because obesity researchers generally don't work on developing better scales for obesity but take the existing scores for granted and test interventions or go for molecular biology.
I think we should look more on how we structure biological knowledge then on testing individual molecular biological hypothesis.
These are all good points. And you're right that A.I. and robotics will come (for a while presumably) in the form of incremental improvements, as they already are.
I guess it feels to me though, like the rate of improvement is basically independent of biology itself, and is determined by the rate at which other fields hand it technology. Sequencing being a good example. We've basically done it to death now, and are waiting for someone to give us better methods that will yield new insights. The major bottleneck at the moment is that we insist on using grad students for manual labor, and nobody has the vision to see that the initial problems in automating basic laboratory tasks would be more than compensated for in the long run, as methods improve, provided there's a collective effort.
I'm also in general not enthusiastic about the many aspects of biology I see, because they seem aimed towards giving incremental life extensions to already affluent and long lived people, at great cost, or of helping a very small number of people at very high cost. Not that these aren't good goals, I just think there's lower hanging fruit.
nobody has the vision to see that the initial problems in automating basic laboratory tasks would be more than compensated for in the long run
That's not true. Peter Thiel's Founders Fund for example backs http://emeraldcloudlab.com/ which automate basic laboratory tasks. They seem to have enough customers to have a waiting list.
I don't see a "Jobs" page on their homepage at first glance, but I would expect that they are a company that can make use of your skills.
It might very well be possible to get a meaningful happiness score out of high resolution GSR data and heart rate data. A few years ago I heard that they manage to do emotional detection with 80% accuracy. Having an objective way to measure happiness on a daily basis would be huge for treating depression and measuring which drug works.
Today's heart rate monitors might not be high accuracy enough, so there's a need to provide applications for higher resolution monitoring to incentivise Apple, Samsung and Microsoft to develop the tech for smartwatches. GSR data is very useless if you don't have an algorithm interpreting it but once you interpret it you can pick up bodily events.
Besides developing the actual hardware developing statistics like that, that provide meaningful insights seems to be important to me. Developing better scales for obesity isn't only about producing new technology but also about analysis of data.
The fact that we have an open access uniprot is also not just about technology. If you look at chemistry where the American Chemical Association claims ownership of CAS numbers, the state of affairs is worse. Thinking about getting more knowledge into a format like uniprot, isn't just about technology but requires thinking about ontology. I like Barry Smiths work in that area.
Thank you, I'd never heard of Emerald Cloudlab. I guess I was speaking too much from my own observations and without enough research.
The fact that you can do your PHD without being aware where real innovation is happening is a good illustration of the poor state of academic biology.
I don't think there are easy solutions for fixing academic biology, but it's an important problem. The key is to step up a meta level. It might be harder to get grants to work on that level but the possible gain is much higher. In some sense the biosafety issues are also up one meta level.
The replicability of papers is significantly hindered by lack of automation, to my mind.
I think the Cloud approach is here really great. In a laboratory you can do things implicitly. In a cloud experiment you have to specify everything explicitly. Emerald Cloudlab allows free hosting of all the experimental data if a researcher makes the data publically available.
First and foremost, don't bother with Java, it'll be dead in 5 years. (Okay, just kidding, sorta.)
Okay, so jokes aside: what do you want? As in, what do you hope that the world will accomplish before you die? Even if you aren't the one who makes the breakthrough, you still benefit. So, what do you hope that someone, anyone, it could be you, it could be some scientist somewhere else, what do you hope they will do, more than anything else?
You seem to point to things that revolve around life extension, and your thought that current methods aren't going to get it done. So, conceptually, what DO you see getting it done? You mention, effective robots to do experiments, and AI to interpret results, but what does that actually mean? What types of experiments? Why a robot instead of a human? As for AI: what results need to be interpreted? What answers are you hoping to find?
I have found that turning a more analytical eye towards your long-term goals, and changing them from purely conceptual to something more actionable, is a great first step for determining what you want to do with your life.
First and foremost, don't bother with Java, it'll be dead in 5 years. (Okay, just kidding, sorta.)
When Python 2.7 (or gasps 2.6) and even COBOL won't die, Java is going to be around for a long time.
I'd much rather learn C++ for all it's faults, since it meshes so nicely with R and Python, but people keep telling me to learn Java...
What I"m referring to in my field specifically is understanding gene regulatory networks. I've become convinced that the only way we're going to get a hold on them is by actually simulating the biochemistry. Searching for higher level abstractions within them just doesn't work that well. This will require lots and lots of experiments, which are currently done by hand, to be automated, and the results to be synthesized into very complex simulations. Humans are too slow, and their minds too small.
As for what I want, that's a good question. I'm not particularly enthusiastic about pouring our resources into tiny, high cost, low quality life extensions, which is what I see most of biology like cancer research, doing now (those parts of it that are aren't just furthering careers). I'd be more enthusiastic about improving quality of life for large numbers of people, or averting catastrophic risks.
There are several organizations around tackling the problem of life extension, have you looked into those?
I have. I'm not wholly decided but as far as I can see the field suffers from most of the same problems that other biological fields do, and is also a bit overcrowded - research funding is pouring into it lately, and I think you could do more good by researching other fields that would feed them better methods, than by working in it directly.
I'm just midway through a masters in bioinformatics, and am currently applying for jobs at deep learning startups, so I'm fairly familiar with AI and genomics.
A few suggestions:
At some point, someone will need to crunch a lot of data in order to create some reliable heuristics by which a majority of virulent DNA could be flagged for further review or quarantine. Preferably the sequences could be uploaded and scanned automatically before they are synthesized. This would go a long way towards reducing a big extinction threat. The first true Virus Scanner?
To be effective, you might need to cooperate with someone who has more technical skills, but your partner would certainly need your assistance to interpret the DNA strands before they could be effective so it is a good match.
Yeah, cognitive genomics could help humans to be smarter when we have to deal with an AI. It could have bad consequences too, mind. There are only some dozens of people who have the guts to work directly on the problem of cognitive genomics, so if you got in this field, you wouldn't have to worry that your research was pointless. Rather, you could become a useful point of contact for people thinking about future tech.
Here are a couple of relevant articles. https://intelligence.org/2013/08/31/stephen-hsu-on-cognitive-genomics/ http://arxiv.org/pdf/1408.3421.pdf
The types of people who change the world through their research or at least make huge progress tend to be the type who naturally focus on and become outright obsessed with a particular unsolved problem, technology or idea.
I think a large part of my lack of enthusiasm comes from my belief that advances in artificial intelligence are going to make human-run biology irrelevant before long.
That may be true, but if so it can be viewed as an opportunity just as much as a threat. If you believe this then go learn some AI - your background in bio could give you a unique perspective. The modern world is all about dual/multi class.
You could probably find some overlap between your current area of expertise and FAI research by bridging with philosophy of psychology, performance psychology, behavioral economics, linguistics, philosophy of language, classification of mental disorders, treatment of mental disorders, positive psychology, happiness economics, organizational psychology, machine learning, decision theory, cognitive psychology, cognitive science or philosophy of science
Does computational neuroscience sound interesting to you?
Seems like a field that could use your stats skills, and understanding how the brain works seems likely to be important for AI.
I think a large part of my lack of enthusiasm comes from my belief that advances in artificial intelligence are going to make human-run biology irrelevant before long.
I suspect that's the issue, and I suspect AI will not be the Panacea you expect it to; or rather, if AI gets to the point of making Human-run research in any field irrelevant - it may well do so in all fields shortly thereafter, so you're right back where you started.
I rather doubt it will happen that way at all; it seems to me in the forseeable future, the most likely scenario of computers and biology are as a force multiplier, allowing processes that are traditionally slow or tedious to be done rapidly and reliably, freeing humans to do that weird pattern-recognition and forecasting thing we do so well.
I should be clearer on that score. It's not that I see a high likelihood of a singularity happening in the next 50 years, with Skynet waltzing in and solving everything. Rather I see new methods in Biology happening that render what I'm doing irrelevant, and my training not very useful. An example: lots of people in the 90s spent their entire PhDs sequencing single genes by hand. I feel like what I'm doing is the equivalent.
I'm a PhD student wrapping up a doctorate in Genomics. I started in biology and switched to analysis because I have stupid hands. My opinion of my field is low. Working in it has, on on the bright side, taught me some statistics and programming. I'm roughly upper 5% on math ability, relative to my college class. Once upon a time I could solve ODEs, now most of my math is gone. However, I'm good with R, and can talk intelligently about mixed linear model, bayesianism vs. frequentism and about genetics, biochemistry and developmental biology. It's also taught me that huge segments of the biology literature are a mixture of non reproducible crap, and uninteresting, street-light science, dressed up as progress with deceptive plots and statistics. I think a large part of my lack of enthusiasm comes from my belief that advances in artificial intelligence are going to make human-run biology irrelevant before long. I think the ultimate problems we're tackling (predicting genotype from phenotype, reliable manipulation of biology, curing cancer/aging/death) are insoluble with our current methods - we need effective robots to do the experiments, and A.I. to interpret the results.
Here's what I want to ask the lesswrong hivemind:
1)Do you agree? Do you think there are important problems being tackled now in biology that someone with my skillset could be useful in? E.g. analyzing the brain with genetics to try and get a handle on how it's algorithms work? (I'm skeptical of this bottom up approach to the brain myself)
2)Do you think there are areas closer to the AI problem (or say, cryonics...) I could be usefully working on?
Sorry for bothering you with my personal problems, but I recall a thread a while ago inviting this sort of thing, so I thought I'd give it a try. I'm leaning towards the default option right now, which is to do some more courses, so I can say, bluff my way through Hadoop and Java, and then see how much cash I can earn in a boring private sector job. However, I'd prefer to do something I find intrinsically interesting.
Edit: Thanks guys - this has already been helpful.