Earth BioGenome Project: Ill-Conceived Megaproject Du Jour

There's been a bit of buzz recently about an unfunded proposal to ultimately sequence every living species on Earth, warming up by sequencing every eukaryotic species, with a targeted cost of $4.8B.  It pains me a bit to write this, but I'm with those who think this is not a wise way to spend money and certainly not likely to work for anywhere near that budget.
I'm working mostly off an article in Science on the proposal, but there's also been quite a bit of Twitter traffic.  The drivers of the idea appear to largely be molecular systematicists and conservation biologists and analogies are made the Human Genome Project (HGP), which they point out seemed technically impractical when originally proposed.  But as touched on in the article, that comparison is specious.  More importantly, the real value and impact of this project appears to be ill-defined.  And the argument for doing this now isn't stated at all.

Again, this is painful.  I have a reputation at work for being "the mad sequencer", earned by leading a bacterial sequencing effort larger than most public efforts and even more so for constantly advocating doing more sequencing.  But that sequencing has a well-defined purpose to advance our drug discovery goals and we have the track record to prove the strategy works.  

I have no doubt that having sequences for all eukaryotes would reveal fascinating biological insights.  But one must weigh that against reasonable alternatives.  There's a strong "build it and they will come" aspect to this proposal, an idea that if all these genomes are available they will attract analysis that yields those insights.  But perhaps it would be better to sequence less and invest more in interpretation?  Or sequence a smaller number of species but more individuals from those species to sample geographic variation? 

There's also a very real question of the quality of sequence.  The number $4.8B is thrown out for the entire project, an inflation-adjusted pricetag from the HGP.  The article also throws out a number of $100 per eukaryotic genome, which a Complete Genomics representative claims they can soon accomplish.  I suspect nobody in the genomics community believes that number; Complete has some serious 'splaining to do.  More importantly, I'd say it's time to really put a stake in the ground and not fund any more short read de novo genomes.

Short read genomes have provided valuable insights, but the reality is that it is abundantly clear that a lot of information is missed.  Human short read sequencing has been successful only because it had a high-quality reference, and these still missed a lot of information.  The sorts of variation missed by short read de novo assembly, repeats, paralogs and details of genome arrangement, are probably often involved in speciation, which is one topic such a grand survey might be expected to shed light on.

Back to that cost; anyone in the industry must be gaping at it.  Let's suppose Complete or Illumina (which made similar claims for some future iteration of NovaSeq) can really deliver appropriate coverage of a typical eukaryotic genome.  We'll ignore for a moment the astounding range of sizes of eukaryotic genomes, which vary about 10,000 fold.  The typical short read metric for resequencing is 30X coverage of a diploid genome; not the 100X typically needed for de novo assembly.

But those cost estimates?  Nearly always they are only data generation.  Maybe library preparation is thrown in, but often not.  Manufacturers can get away with this less-than-honest pricing, but a major project needs to consider fully loaded costs.  Every cost needs to go in: DNA extraction, quality control, analysis, data storage.  Costs of failures.  The science article cites 1.5 million eukaryotic species, which seems really low.  Especially when I can find an estimate of over 5 million fungal species and one paper that suggests there may be 1.6 million protists (most of which have not yet been cataloged). But let's work off that estimate of 1.5 million -- that averages out to about $3K per species for a $4.8B budget.  So they're not relying on that bargain basement $100 per genome price.  But again, that needs to cover everything.

The real budget-buster may well be getting all the required DNA.  Stored specimens may not be suitable; new collections may need to be executed (and funded).  This is the most gigantic difference between this proposal and the HGP: the HGP needed to start with a small number of DNA samples from one species, easily obtainable.  In contrast, the BioGenome proposal requires extracting and tracking millions of samples from a wide array of different sorts of organisms.

Then there's the issue of quality control; without care this effort could spawn hundreds or even thousands of tardigates.  If you don't recognize that jargon, the first paper to report a genome sequence for a tardigrade (water bear) claimed to have found widespread horizontal transfer into the genome.  The second tardigrade genome paper failed to find such and the initial assembly was later shown to be seriously incorrect and marred by contaminants.  If you aren't funding detailed analysis, which is expensive, this sort of garbage-in, garbage out fiasco awaits.

The BioGenome proponents try to channel the spirit of the HGP and say that it too seemed infeasible when launched.  But there's a chasm of difference: HGP and later development focused on first solving a technical challenge which wasn't clearly solvable and then focused on reducing costs.  The huge cost reductions have come after the HGP with modern sequencing instruments, which have enabled eliminating gigantic rooms full of incubators, colony pickers, prep robots and the like.  The first human genome was generated by an army of individuals working in multiple huge facilities on multiple continents.  In contrast, one could probably set up a facility to generate platinum genomes in a two-car garage.

Unfortunately, what BioGenome needs to improve on are mostly hard, logistical problems that don't lend themselves to automation or miniaturization. This is the problem all of genomics is starting to run into: the sequence generation may soon be just a sliver of the total cost and effort of any sequencing project.  That sliver will continue to shrink as technology improves, but all the remaining cost and effort will be very hard to improve upon.

What's the alternative?  Let's start by requiring platinum quality, not pewter, quality genomes, with full blown analysis. I don't have a great handle on what that would cost, but let's throw out a range of $20K to $50K.  Let's also stipulate that this is going to be hard to chisel down; much of that cost is going to be the analysis.  By platinum genome we mean one which resolves, with a low level of exception, each chromosome arm as a set of haplotype-resolved contigs and represents the genetic variation in the source sample and an error rate below one error per megabase (I'm guessing on that error rate).  That's going to mean high quality input DNA, which will probably rule out museum specimens. It's going to mean a minimum of long read sequencing, optical mapping and some sort of Hi-C mapping.  Perhaps some of the smallest genomes can be solved purely with long read sequencing.  

That would ensure high quality genomes that should stand the test of time, but with the cost I am suggesting a $4.8B megaproject would be sequencing only about 100K-200K genomes.  That's still an awful lot of genomes, but really good ones.  These genomes will also save researchers from making silly mistakes or not being able to make solid conclusions due to uncertainty in the data.  And to reiterate, the fully loaded costs of these genomes is going to be dominated by sample collection, quality control, analysis and such, so it's worth amortizing those costs over higher quality information that has permanent value.

But that still begs the question of whether this is a good use of research funds.  For example, the Science article marks the number of eukaryotic families at about 9000.  So $450M might give platinum membership to each eukaryotic family.  That's already a large chunk of change, but perhaps justifiable to place benchmarks around the eukaryotic tree.  But that's only 10% of what is proposed; rationalizing the remaining bit to generate sequences to fill out the tree is going to be difficult.  

Now, the BioGenome project doesn't plan to replicate other projects.  There's the 10,000 Vertebrate Genomes and various other "N of X" genome projects.  Which I glumly suspect are also tending to generate short read assemblies.  Which is a reminder of a serious flaw in these catchy names: if you later realize it made more scientific sense to sequence fewer genomes to higher quality (or fewer species and more individuals per species), you're a bit hemmed in by your name.  So, according to this logic, rather than yet another "N of X" short read scheme I'd much prefer to hear a proposal for "An Inordinate Number of Fondly Sequenced Beetle Genomes".