I'm at the 2014 Marine Microbes Gordon Conference right now, and at the end of my talk, I brought up the point that the function of most genes is unknown. It's not a controversial point in any community that does environmental sequencing, but I feel it should be mentioned at least once during every session on metagenome sequencing :).
The lack of functional information for the vast majority of genes is, in my view, the broadest and biggest challenge facing environmental microbiology. Known colloquially as "microbial dark matter" (ref and Nature News), it is fair to say that we have virtually no window into what the majority of genes do. This is particularly a problem now that we can readily access them with sequencing, and several fields are racking up hundreds or thousands of data sets that are largely uninterpretable from a functional perspective.
So what are our options? What can we do to characterize new genes? There seem to be two poles of opinions: many experimentalists argue that we need to devote significant efforts to doing more microbial physiology, which is, after all, how we know most of what we already know. People at the other pole seems to think that if we do enough sequencing, eventually meaning will emerge - enough correlations will turn into causation. (While these are obviously caricatures, I think they capture most of the range of opinions I've heard, so I like 'em ;).
Neither course seems likely to me. Nobody is going to fund hundreds or thousands of graduate student projects to characterize the physiology of individual microbial species, which is more or less the scale of effort needed. Similarly, while the sequencing folk have clearly been "winning" (in the sense that there's a lot of sequencing being done!) there's a growing backlash against large-scale sequencing without a fairly pointed set of hypotheses behind them. This backlash can be understand as a natural development -- the so-called trough of disillusionment in the adoption and understanding of new technologies -- but that makes it no less real.
Over the past few years, I've had the opportunity to discuss and debate a variety of approaches to characterizing gene function in microbes. Since I'm thinking about it a lot during this meeting, I thought I'd take the time to write down as many of the ideas as I can remember. There are two purposes to this -- first, I'm trawling for new ideas, and second, maybe I can help inspire people to tackle these challenges!
Without further ado, here is my list, broken down into somewhat arbitrary categories.
Experimental exploration and determination of gene function
Finding genetic systems and doing the hard work.
This is essentially the notion that we should focus in on a few model systems that are genetically tractable (culturable, transformable, and maybe even possessed of genome editing techniques) and explore, explore, explore. I'm not sure which microbes are tractable, or could be made tractable, but I gather we are lacking model systems representative of a broad swath of marine microbes, at least.
The upsides to this approach are that we know how to do it, and all of the modern -omics tools can be brought to bear to accelerate progress: genome, transcriptome, and proteome sequencing, as well as metabolomics.
The downsides are that this approach is slow to start, time consuming, and not particularly scalable. Because of that I'm not sure there's much support for funding.
Transcriptome assisted culture.
A persistent challenge for studying microbes is that many of them cannot be easily cultured, which is a soft prerequisite for studying them in the lab. We can't culture them because often we don't know what the right culture conditions are -- what do they eat? Who do they like to hang out with?
One of the neater approaches to resolving this is the concept of transcriptome assisted culture, which Irene Newton (@chicaScientific) pointed out to me in this neat PNAS paper on culturing Coxiella. Essentially, Omsland et al. used transcriptome sequencing in conjunction with repeated modifications to the culture medium to figure out what the right growth medium was. In addition to converting an important biomedical pathogen into something more easily culturable, the authors gained important insights into its basic metabolism and the interaction of Coxiella with its host cells.
Upsides? It's an approach that's readily enabled by modern -omics tools, and it should be broadly applicable.
Downsides? Time consuming and probably not that scalable. However, it's a rather sexy approach to the hard slog of understanding organisms (and you can argue that it's basically the same as the model organism approach) so it's marginally more fundable than just straight up physiology studies.
Another culture-based approach is the enrichment culture, in which a complex microbial community (presumably capable of driving many different biogeochemical processes) is grown in a more controlled environment, usually one enriched for a particular kind of precursor. This can be done with a flow reactor approach where you feed in precursors and monitor the composition of the outflow, or just by adding specific components to a culture mix and seeing what grows.
For one example of this approach, see Oremland et al., 2005, in which the authors isolated a microbe, Halarsenatibacter silvermanii, which metabolized arsenic. They did this by serial transfer of the cells into a fresh medium and then purifying the organism that persistently grew through serial dilution at the end.
This is a bit of a reverse to the previous methods, where the focus was on a specific organism and figuring out how it worked; here, you can pick a condition that you're interested in and figure out what grows in it. You can get both simplified communities and potentially even isolates that function in specific conditions. (Also see Winogradsky columns for a similar environment that you could study.) You still need to figure out what the organisms do and how they do it, but you start with quite a bit more information and technology than you would otherwise - most importantly, the ability to maintain a culture!
Pros: this is actually a lot more scalable than the model-organism or culture-focused techniques above. You could imagine doing this on a large scale with a fairly automated setup for serial transfer, and the various -omics techniques could yield a lot of information for relatively little per-organism investment. Someone would still need to chase down the genes and functions involved, but I feel like this could be a smallish part of a PhD at this point.
Cons: it's not terribly hypothesis driven, which grant agencies don't always like; and you might find that you don't get that much biological novelty out of the cultures.
You can also understand what genes do by putting them into tractable model organisms. For example, one of the ways that Ed DeLong's group showed that proteorhodopsin probably actually engaged in photosynthesis was by putting the gene in E. coli. At the time, there was no way to investigate the gene (from an uncultured SAR86) in its host organism, so this was the only way they could "poke" at it.
A significant and important extension of this idea is to transfer random fragments from metagenomic fosmid or BAC libraries into large populations of (say) E. coli, and then do a selection experiment to enrich for those critters that can now grow in new conditions. For example, see this paper on identifying the gene behind the production of certain antibiotics (hat tip to Juan Ugalde (@JuanUgaldeC for the reference). Also see the "heterologous expression" paragraph in Handelsman (2004), or this other antibiotic resistance paper from Riesenfeld et al. (2004) (hat tips to Pat Schloss (@Pat Schloss), Jeff Gralnick (@bacteriality), and Daan Speth (@daanspeth) for the refs!).
Pros: when it works, it's awesome!
Cons: most genes function in pathways, and unless you transfer in the whole pathway, an individual gene might not do anything. This has been addressed by transferring entire fosmids with whole operons on them between microbes, and I think this is still worth trying, but (to me) it seems like a low-probability path to success. I could be wrong.
Why not just build a new critter genome using synthetic biology approaches, and see how it works? This is a radical extension of the previous idea of transferring genes between different organisms. Since we can now print long stretches of DNA on demand, why not engineer our own pathways and put them into tractable organisms to study in more detail?
I think this is one of the more likely ideas to ultimately work out, but it has a host of problems. For one thing, you need to have strong and reliable predictions of gene function. For another, not all microbes will be able to execute all pathways, for various biochemical reasons. So I expect the failure rate of this approach to be quite high, at least at first.
Pros: when it works, it'll be awesome! And, unlike the functional metagenomics approach, you can really engineer anything you want - you don't need to find all your components already assembled in a PCR product or fosmid.
Cons: expensive at first, and likely to have a high failure rate. Unknown scalability, but probably can be heavily automated, especially if you use selection approaches to enrich for organisms that work (see previous item).
Computational exploration and determination of gene function
Look at the genome, feed it into a model of metabolism, and try to understand what genes are doing and what genes are missing. Metabolic flux analysis provides one way to quickly identify whether a given gene complement is sufficient to "explain" observed metabolism, but I'm unsure of how well it works for badly annotated genomes (my guess? badly ;).
You can marry this kind of metabolic analysis with the kind of nifty fill-in-the-blank work that Valerie de Crecy-Lagard does -- I met Valerie a few years back on a visit to UFL, and thought, hey, we need hundreds of people like her! Valerie tracks down "missing" pathway genes in bacterial genomes, using a mixture of bioinformatics and experimental techniques. This is going to be important if you're predicting metabolic activity based on the presence/absence of annotated genes.
In practice, this is going to be much easier in organisms that are phylogenetically closer to model systems, where we can make better use of homology to identify likely mis-annotated or un-annotated genes. It also doesn't help us identify completely new functions except by locating missing energy budgets.
Pros: completely or largely computational and hence potentially quite scalable.
Cons: completely or largely computational, so unlikely to work that well :). Critically dependent on prior information, which we already know is lacking. And hard or impossible to validate; until you get to the point where on balance the predictions are not wrong, it will be hard to get people to consider the expense of validation.
Gene-centric metabolic modeling
Rather than trying to understand how a complete microbe works, you can take your cue from geochemistry and try to understand how a set of genes (and transcripts, and proteins) all cooperate to execute the given biogeochemistry. The main example I know of this is from Reed et al. 2013, with Julie Huber (@JulesDeep) and Greg Dick.
Pros: completely or largely computational and hence potentially quite scalable.
Cons: requires a fair bit of prior information. But perhaps easier to validate, because you get predictions that are tied closely to a particular biogeochemistry that someone already cares about.
Sequence everything and look for correlations.
This is the quintessential Big Data approach: if we sequence everything, and then correlate gene presence/absence/abundance with metadata and (perhaps) a smattering of hypotheses and models, then we might be able to guess at what genes are doing.
Aaron Garoutte (@AaronGoroutte) made the excellent point that we could use these correlations as a starting point to decide which genes to invest more time and energy in analyzing. When confronted with 100s of thousands of genes -- where do you start? Maybe with the ones that correlate best with the environmental features you're most interested in ...
Pros: we're doing the sequencing anyway (although it's not clear to me that the metadata is sufficient to follow through, and data availability is a problem). Does not rely on prior information at all.
Cons: super unlikely to give very specific predictions; much more likely to provide a broad range of hypotheses, and we don't have the technology or scientific culture to do this kind of work.
Look for signatures of positive selection across different communities.
This is an approach suggested by Tom Schmidt and Barry Williams, for which there is a paper soon to be submitted by Bjorn Ostman and Tracy Teal et al. The basic idea is to look for signatures of adaptive pressures on genes in complex metagenomes, in situations where you believe you know what the overall selection pressure is. For example, in nitrogen-abundant situations you would expect different adaptive pressures on genes than in more nitrogen-limited circumstances, so comparisons between fertilized and unfertilized soils might yield something interesting.
Pros: can suggest gene function without relying on any functional information at all.
Cons: unproven, and the multiple-comparison problem with statistics might get you. Also, needs experimental confirmation!
My favorite idea - a forward evolutionary screen
Take fast evolving organisms (say, pathogens), and evolve them in massive replicate on a variety of different carbon sources or other conditions (plates vs liquid; different host genotypes; etc.) and wait until they can't cross-grow. Then, sequence their genomes and figure out what genes have been lost. You can now assume that genes that are lost are not important for growing in those other conditions, and put them in a database for people to query when they want to know what a gene might not be important for.
We saw just this behavior in Campylobacter when we did serial transfer in broth, and then plated it on motility assay plates: Campy lost its motility genes, first reversibly (regulation) and then irreversibly (conversion to pseudogene).
Harriet Alexander (@nekton4plankton) pointed out to me that this bears some similarity to the kinds of transposon mutagenesis experiments that were done in many model organisms in the 90s - basically, forward genetics. Absolutely! I have to think through how useful forward genetics would be in this field a bit more thoroughly, though.
Pros: can be automated and can scale; takes advantage of massive sequencing; should find lots of genes.
Cons: potentially quite expensive; unlikely to discover genes specific to particular conditions of interest; requires a lot of effort for things to come together.
So that's my list.
Can't we all get along? A need for complementary approaches.
I doubt there's a single magical approach, a silver bullet, that will solve the overall problem quickly. Years, probably decades, of blood, sweat, and tears will be needed. I think the best hope, though, is to find ways to take advantage of all the tools at our disposal -- the -omics tools, in particular -- to tackle this problem with reasonably close coordination between computational and experimental and theoretical researchers. The most valuable approaches are going to be the ones that accelerate experimental work by utilizing hypothesis generation from large data sets, targeted data gathering in pursuit of a particular question, and pointed molecular biology and biochemistry experiments looking at what specific genes and pathways do.
How much would this all cost?
Suppose I was a program manager and somebody gave me \$5m a year for 10 years to make this happen. What would be my Fantasy Grants Agency split? (Note that, to date, no one has offered to give me that much money, and I'm not sure I'd want the gig. But it's a fun brainstorming approach!)
I would devote roughly a third of the money to culture-based efforts (#1-#3), a third to building computational tools to support analysis and modeling (#6-#9), and a third to developing out the crazy ideas (#4, #5, and #10). I'd probably start by asking for a mix of 3 and 5 year grant proposals: 3 years of lots of money for the stuff that needs targeted development, 5 years of steady money for the crazier approaches. Then I'd repeat as needed, trying to balance the craziness with results.
More importantly, I'd insist on pre-publication sharing of all the data within a walled garden of all the grantees, together with regular meetings at which all the grad students and postdocs could mix to talk about how to make use of the data. (This is an approach that Sage Biosciences has been pioneering for biomedical research.) I'd probably also try to fund one or two groups to facilitate the data storage and analysis -- maybe at \$250k a year or so? -- so that all of the technical details could be dealt with.
Is \$50m a lot of money? I don't think so, given the scale of the problem. I note that a few years back, the NIH NIAID proposed to devote 1-3 R01s (so \$2-4m total) to centers devoted to exploring the function of 10-20 pathogen genes each, so that's in line with what I'm proposing for tackling a much larger problem.