In 2007 I was asked to write a chapter in protein comparative modeling. At the time, the PSI was churning out lots of protein structures, of which roughly 20% corresponded to new CATH and/or SCOP folds. Based on this performance, I could write with some degree of confidence that a concerted effort was underway to produce a truly representative sampling of protein conformational space that might some day become a comprehensive basis for comparative modeling of effectively the entire plausible proteome.
This written, I put the blinders on and went back to my focus on in silico drug design. Meaning, of course, that I spent most of my time looking at a fairly narrow subset of the fold realm, corresponding to established targets and their close relatives. In the back of my mind, though, I more or less assumed that the PSI was continuing to churn out great new advances in fold discovery.
Now, having been asked to write an update to the chapter, I am surprised to discover that no new folds have been registered in CATH since 2009, and that there's been nothing new in SCOP since 2008!
So my question is this: has the world (and PSI in particular) de-emphasized novel fold discovery to the point of near abandonment, or does it appear that all the low-hanging fruit have been plucked and that the remaining portion of uncharacterized distinct structure space (estimated to be perhaps 700 folds) corresponds to problematic structures with poor analytical prognosis (e.g., poor solubility; inherent disorder, etc.)?
Clearly I would have preferred to answer this through literature survey rather than taking up your valuable time, but in my initial forays I haven't been able to come up with any clear resolution, perhaps because most scientists tend not to emphasize failures or topics that they've stopped pursuing. So, any thoughts?
With your permission, I would be happy to explicitly cite any of you who can shed light on this.
Thanks!
I would like to add a minor clarification: the statement above that CATH had not been updated since 2009 was based on examination of the CATH-related statistics reported on the PDB site. Not reflected on PDB were 31 new folds that were characterized through 2011. Obviously that is a smaller rate of discovery than had previously been the case. I have still not found evidence of novel SCOP characterization post 2008 however.
Hi Gerald. There is no recent update of SCOP hence no new folds. CATH published an update I think in NAR this year, but I can't remember which PDB version they were aligned to. In any case they reported a steadily declining new fold discovery rate, except for membrane proteins.
As for the main question, I have close interactions with the coordinator of NESG, and they have greatly de-emphasized new folds. I think it was indeed an NIH indication. The new focus is biologically/biomedically relevant problems, largely through collaborations with non-SG research teams. I think the current model is that biologists with challenging issues that 3D structures could help disentangle walk up to the SG centers and ask them to solve a number of structures e.g. in a pathway. SG centers also have the possibility to choose their own targets but, as I mentioned, NIH prefers these to be biologically/biomedically relevant - except when it comes to methods development, but also there new folds are typically not the first choice.
I assume NIH wants more bang for their buck in terms of practical applications (human health) and new folds from exotic bugs are not really of interest, (well, if it's proteins from the flu virus then it's another story!)
Excellent -- thank you for the detailed insight! That is largely as I expected.
The goal of the NIGMS Protein Structure Initiative - even at the very beginning - was not to 'discover new folds'. New fold discovery occurred as a natural consequence of the huge increase in the number of protein structures that were determined. If you plot the number of new folds discovered versus time, you will see an asymptote. I think that the reason that no new folds are being documented in SCOP has more to do with SCOP no longer being actively maintained and updated by its creators, than anything else. CATH is being actively updated.
Antonio's point about the NIH not wanting 'new folds from exotic bugs' completely misses the point. And actually the 'exotic bugs' that certain groups focused on were human pathogens!
Perhaps I did not make myself clear: as I mentioned, if it's a human pathogen (e.g. flu virus) it is still of interest. Nevertheless, I am pretty sure, as at the time I was following things closely from the European side of it and had some meetings with the NIH person in charge, that the first phases focused explicitly on high-throughput technology development and fold space coverage. You can see in the literature a number of bioinformatics papers describing strategies to pick proteins to efficiently sample fold space in the context of SG. The third phase has markedly shifted away from this to go into collaborative efforts to ensure that systems of broad interest are tackled.
Notably, the only European SG project, SPINE, started later than PSI and from its beginning focused on biomedical relevant targets, partly because the criticism that new folds were interesting but not particularly useful was already around at that time.
Oh, I think it is fair to mention that the PSI people are still solving a number of structures for initiatives such as CASP or CASD-NMR, which I presume are difficult to predict (no obvious homologue in the PDB) even though they many not be new folds. However, I'd classify them as an effort primarily aimed at methods development rather than new fold discovery.
I too am part of the PSI - Antonio has it right, but I'd like to add a few thoughts.
To answer your original question, yes, PSI has de-emphasized it. But it's not a big secret... You can see from the RFAs that % effort on novel folds was reduced dramatically (I think to 15%?) to provide resources to study more biologically relevant proteins and protein complexes. There were three reasons for this: (1) a majority of the folds that were determined during the PSI-2 period ended up being variants of known folds - oh well, we had to look to know that. (2) a relatively narrow population of the scientific community cares about folds, when it's the surface that's of functional relevance, and obviously the whole protein that is of biological relevance (3) the average taxpayer certainly does not care about folds and the theoretical models they leverage, but about direct biology and new drugs. When a project is supported with hundreds of millions of dollars, impact on the lay community is obviously a huge concern for us.
Aside from the lack of a SCOP update, I know that the PSI JCSG group has been actively working with Pfam on the novel domain sequences (not so much folds) they've found. You can speak with Adam Godzik on that matter.
Hi,
Thanks for these v interesting comments. I thought I'd drop a few lines as sbdy who's trying to discover new folds. I work on proteins originated de novo (ie from scratch, not by duplication, fusion or fission from existing proteins) in viruses. We suspect such proteins tend to have previously unknown folds because the two ones whose structure has been solved so far both have completely new folds and new mechanism of action (tombusvirus p19, which blocks RNA interference, and SARS coronavirus ORF9b, of unknown function). See discussion of Rancurel et al J Virol 2009 for more precise description and references.
My project involved trying to solve the 3Dd structure of proteins originated de novo and see whether they have new folds or known folds, and certainly it was made clear that solving new folds per se is not deemed valuable anymore. However of course, we're trying to do sth different, not just find new folds per se: we're doing a new, experimental approach to understanding the age-old problem of why we observe a limited number of folds. Indeed, if proteins originated de novo have previously known folds, this proves that the number of viable folds in nature really is constrained (and also proves unambiguously that convergent evolution at the fold level is possible, sth v difficult to do). However, if proteins originated de novo have folds that we hadn't observed so far, it means that 1) the number of viable folds is not as limited than we thought - we're probably underestimating it because of our poor knowledge of proteins originated de novo; 2) the reason why the number of folds is small, regardless, is probably because protein de novo origination is rare - most proteins existing today were generated by a LOT of duplication from a FEW folds... Does that make any sense?
Problem is, as you hinted, viral proteins originated de novo are very hard to work with (attrition rate 99.5%) and poorly studied. And I've been really struggling to produce them. Ongoing.
Hope that answers part of your question...
PS: the reason we're sure these proteins originated de novo (as opposed to have diverged beyond recognition) is because they overlap, in a different reading frame, other genes which have a much wider phylogenetic distribution (they originated by "overprinting" -see Rancurel J Virol 2009). Another case you can be sure is if they originated from conserved intergenic region (in some species, the intergenic region have stop codons but not in those encoding these proteins). The field of de novo protein origination is just taking off(The evolutionary origin of orphan genes, Nat Rev Gen 2011), so maybe there will be some structures solved in a few years... If you guys want to solve some you can't go wrong there, nobody's working on that at present except in viruses!
David -- thank you for the enlightening discussion on a facet of the field that I was only peripherally aware of!
At the risk of pointing you toward something that you were already aware of, a couple weeks ago at Proteomics 2013 I attended a talk by Michael Hecht (Princeton) which discussed the folding capacity of artificially synthesized proteins specified based on random sequence specification, but subsequently filtered by some empirical rule he'd developed to select for sequences with innate propensity to fold (e.g., presence of a hydrophobic core, sufficient composition of subsequences with plausible helix or sheet propensities).
The three highlights of Hecht's work were a) that these artificial sequences that met their basic predictive for folding did, by and large, proceed to fold fairly well and produce structures that were vaguely reminiscent of real biological globular proteins, b) the completely artificial proteins proved to be viable 'food' for E. coli, and c) the proteins often folded in a manner as to attain semi-selective small molecule binding sites (as measurable from chemical screening experiments).
I would assume that folding stability is likely only a minor component of the attrition that you encounter in your work, but it's possible that Hecht's in-house method for predictive prescreening according to amenity to folding might help to streamline your efforts?
Hi Gerald, thank you very much! Will follow that up! Thing is, I use high-throughput technologies and put pretty much all proteins I can find in the pipeline - barely costs more, so I don't need to prescreen candidates (as long as they're not predicted to be disordered). I mean of course it may decrease the attrition rate (if I put in less sequences) but it won't decrease the toal number of targets that are soluble/put in xtallization trials (since I try all of them) or really save time or money. And basically no method to predict xtallization is really proven on these difficult proteins, so I'd hesitate anyway to test this new method. HOWEVER, I think it's very interesting for the study of proteins originated de novo (be it in nature or by human design) and will follow the paper/subject up! thanks D
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