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 : [email protected]
<mailto:[email protected]>
phone : +31-30-2532865
fax : +31-30-2533940
__________________________________________
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