I would like to thank everyone who took the time to respond to my
question that started this thread. It is really good for me to get a
sense of the community perspective. Some debates were predictable,
others not. Many ideas I agree with, some not so much. All were
thought-provoking. I think this is going to be a really good GRC!
Something I did not expect to distill from all the responses is that the
dominant challenge in structural biology is financial. The most common
strategy suggested for addressing this challenge was torpedoing other
scientists in similar fields, perhaps expecting to benefit from the
flotsam. Historically, this strategy is often counterproductive and at
best inefficient. The good news is there is a lot of room for
improvement. In reality, we are all on the same ship, and the people in
our funding agencies fighting to get us what we need can be much more
effective when armed with positive ideas and clear plans. That is a
better strategy for overcoming this challenge.
To this end, my first GRC session title is going to be:
"If I had a trillion dollars for structural biology"
I think we can all agree that science in general is vastly under-funded
relative to the impact it has on the human condition. For example, I
estimate the value of a general cure for cancer to be at least a
trillion dollars. This is based on the lives claimed every year,
multiplied by how much one person would gladly pay after being diagnosed
(amortized over the rest of their much longer life). This is only ~1% of
the Gross World Product, a real bargain if we can come up with a plan
that will actually work.
Now, obviously not all cancer research is structural biology, but not
all structural biology is cancer research either. Let us suppose for a
moment that you (yes, I'm talking to YOU), were given a trillion-dollar
budget to do your science. After buying all the tools and hiring all
the people you wanted: would that solve all of your problems? I expect
not. The intellectual and technical challenges that remain are what I
believe science is really all about, and the 2020 Diffraction Methods
GRC will focus on the ones facing structural biology.
My goals here are twofold:
1) I believe it would be healthy for this field if we all spent a little
time "thinking big"
2) I want to remove financial anxiety from the discussion, both here and
at the GRC.
I ask for one restraint: please confine the discussion to structural
biology. I understand it is difficult to think about the
trillion-dollar level without involving politics, but the CCP4 Bulletin
Board is not a political discussion forum, and neither is the GRC.
Assume all the other worthy causes in the world are given their own
ample budgets. This trillion is yours, and you have to spend it on
structural biology. If you can't think of anything, think harder.
To get you started, a few things that could be done for under a trillion
dollars:
1) re-do all the protein crystallization in the PDB, 500 times (saving
all information)
2) buy Google and Facebook, get their AI teams to do machine learning
and structure prediction for us
3) hire every "biological scientist" in the world, and give each $1M to
work on your projects
4) re-do the NASA Apollo program three times
5) build 1000 XFELs and 100,000 Titan microscopes (yes, that's "and")
6) solve the phase problem by brute force. (zettaflops-scale computing
at $0.03/gflop)
7) build half a dozen terapixel detectors (ask Colin Nave what those can do)
8) fund every NIH grant submitted in the last 5 years. Not just the
awarded ones, all of them.
9) X-prize style competitions for landmark achievements, such as
predicting crystallization outcomes, or finding a universal way to stop
protein from denaturing on the air-water interface.
This is not a to-do list, but rather an attempt to convey the scale of
what can be done. Oh, and you have a month or so to think about it. The
meeting is July 26-31 2020, but my speaker list is due Oct 15.
Now, of course, at the GRC I will not actually have billion-dollar
prizes to pass around, but I do want to set our sights on those lofty
goals, and then work on the bridge we will need to get there.
So, when I say "challenge" I mean more than something we all agree is
hard. Those would make for very short talks. I am after something more
like a benchmark. Useful challenges should have certain properties.
They should be:
a) possible, because something that doesn't work no matter what you do
is no fun.
b) hard, because something that is too easy is also not very interesting
c) realistic, as in relevant to a real-world problem we all agree is
important
d) accessible, as in reasonable download sizes and/or affordable reagents
e) fast, because it if takes forever to try it nobody will have time to
participate
f) measurable, as in having a clear and broadly acceptable "score"
g) adjustable, as in the level of "difficulty" can be selected
continuously between "easy" and "impossible".
This last one is important because it is at the transition point between
success and failure that teaches us the most about what can be improved.
Some challenges that already exist are:
anomalous phasing from weak signals
https://bl831.als.lbl.gov/~jamesh/challenge/anom/
anomalous phasing from twinned data
https://bl831.als.lbl.gov/~jamesh/challenge/twin/
merging highly incomplete data with an indexing ambiguity
https://bl831.als.lbl.gov/~jamesh/challenge/microfocus/
extracting motions from diffuse scatter data
https://bl831.als.lbl.gov/~jamesh/challenge/diffuse/
Coming soon:
dial-a-resolution model building challenge
XFEL data processing reference set
-James Holton
MAD Scientist
On 7/25/2019 10:07 AM, Keller, Jacob wrote:
>>It would seem to me that an important issue is also: do get all
information out of our diffraction data? By integrating the Bragg
peaks we usually neglect the diffuse scattering that could potentially
contain additional (dynamic) structural information. This can be
cloudy diffuse scattering hidden in the background but also diffuse
streaks that contain information on packing disorder and reveals
intrinsic interactions in the crystal.
Along these lines, and taking a page from you also, how about
“crystallographic model refinement as image-faking?” Metrics of the
goodness of a particular refinement could simply be some measure of
the correlation between predicted vs. measured images. I have seen
some of this done with diffuse scattering, but why not with the whole
thing, including intensity and shape of Bragg peaks, solvent rings,
etc? Maybe instead of doing the multiple steps of (indexing,
integration, scaling, solving…) all of this could be refined as one?
Processing parameters like moscaicity [sic] etc would now be part of
the final model…?
JPK
Loes Kroon-Batenburg
On 07/15/19 21:44, Holton, James M wrote:
Hello folks,
I have the distinct honor of chairing the next Gordon Research
Conference on Diffraction Methods in Structural Biology (July 26-31
2020). This meeting will focus on the biggest challenges currently
faced by structural biologists, and I mean actual real-world
challenges. As much as possible, these challenges will take the
form of
friendly competitions with defined parameters, data, a scoring
system,
and "winners", to be established along with other unpublished results
only at the meeting, as is tradition at GRCs.
But what are the principle challenges in biological structure
determination today? I of course have my own ideas, but I feel
like I'm
forgetting something. Obvious choices are:
1) getting crystals to diffract better
2) building models into low-resolution maps (after failing at #1)
3) telling if a ligand is really there or not
4) the phase problem (dealing with weak signal, twinning and
pseudotranslation)
5) what does "resolution" really mean?
6) why are macromolecular R factors so much higher than
small-molecule ones?
7) what is the best way to process serial crystallography data?
8) how should one deal with non-isomorphism in multi-crystal methods?
9) what is the "structure" of something that won't sit still?
What am I missing? Is industry facing different problems than
academics? Are there specific challenges facing electron-based
techniques? If so, could the combined strength of all the world's
methods developers solve them? I'm interested in hearing the
voice of
this community. On or off-list is fine.
-James Holton
MAD Scientist
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__________________________________________
Dr. Loes Kroon-Batenburg
Dept. of Crystal and Structural Chemistry
Bijvoet Center for Biomolecular Research
Utrecht University
Padualaan 8, 3584 CH Utrecht
The Netherlands
E-mail : l.m.j.kroon-batenb...@uu.nl <mailto:l.m.j.kroon-batenb...@uu.nl>
phone : +31-30-2532865
fax : +31-30-2533940
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