To Properly Assess Cancer Genomics, One Cannot Dismiss It

Through a happy series of professional events, I now get to have lunch very regularly with the author of the excellent blog The Curious Wavefunction.  If you haven't visited there, Ash not only delves into chemistry but the history of science.  In a most friendly way, he dropped a challenge on my Twitter-step that represents a long procrastinated blogging project, so I really couldn't turn it down.  And that challenge is: what has been the value of cancer genomics. Is it, as he asked, a very expensive exercise in looking for keys under the lamppost, or something far more valuable?
Now, to properly assess that question really requires someone steeped in the field, and while that was certainly true when I was back at Infinity, Indeed, I dared to write a review on the topic. I've had a more casual relationship since signing onto my current gig, as I've needed to dive deeply into the world of natural product biosynthesis and genome assembly.  A really proper look at the subject would need a lot of focus by someone skilled at examining the different papers and the competing world of other approaches to learning the roots of cancer.  Alas (but good for my bank account), an Uber for scientific historians does not exist, and I can't realistically engage such a project.  So my imperfect synthesis of the field will have to do -- and as always, I invite those who can spot my errors to please point them out.  So I am relying on rebooting some memory cells and some quick searches of PubMed.  The latter is daunting: "exome AND cancer" brings back 1134 citations at one point in this piece's drafting (likely higher when I publish it); many of those are not in my scope, but quite a large fraction are.

A particularly difficult challenge that would require such focused study would be to disentangle which discoveries can really be credited to various cancer genome projects, and which are rightfully assigned to smaller scale projects.  Sometimes it is easy: the early work on retroviral oncogenesis left many colorful gene names, such as Ras and Myc and Erb which mark them.  Other whimsical names, such as hippo and hedgehog from Drosophila biology.  Sometimes these mix in strange ways.  The viral work gave us the Yes oncogene and later work a binding protein called YAP (Yes-associated protein). Drosophila geneticists found the receptor for YAP and named it Yorkie (a nomenclature Miss Amanda objects to as a slur against some of her close friends).  Other important cancer work has come from studying the cell cycle in yeast, making knockouts and knock-ins in mice and a myriad of other techniques.  

Ash looks a bunch at a piece from 2013 by Mike Yaffe, a well-respected cancer biologist, which laments the vast sums of money that went into cancer genomics.  The underlying assumption, which I will provisionally accept, is that this money could have gone instead to a lot of smaller, individual investigator grants.  Yaffe ends up concluding: "But these efforts have largely ended up finding more of the same".

That is a trope I've heard often from critics of big funding from cancer genomics, but one I would vigorously dispute.  I find it a very unfortunate conclusion, as it effectively shuts down any nuanced discussion of the value of the cancer genome projects.  To me, and admittedly I am a true believer, the cancer genome projects have delivered great insights into cancer, and most importantly ones which can both guide the pharmaceutical industry to deliver drugs for the future , as well as in influence the treatment of cancer in the present.

I've had a recent personal reminder on that last point.  A good friend of mine, whose eldest son is not much older than my own offspring, has been diagnosed with a rare subtype of a common cancer.  I've tried, without being a noodge, to give advice and support.  This is not the first time my life has been touched by cancer -- my paternal grandmother died of leukemia in the 40's, my wife lost an uncle to pancreatic cancer and I lost a dear uncle to multiple myeloma.  Cancer is a fascinating subject, but many fascinating subjects exist which don't involve death and suffering.  The issue of where resources are best spent is not an academic one.

More of the Same Isn't Really More of the Same

So what have the many cancer genomes delivered?  Just to try to be clear on definitions, I include in this space any effort using microarrays or sequencing to explore DNA or RNA changes on tumor samples, and with the exception of a few early, pilot studies for whole genome sequencing these involve many clinical samples.  So while they are interesting, I'm not including GWAS looking for susceptibility loci.  Nor am I including other types of big data cancer studies, such as huge shRNA/RNAi screens or now the emerging studies using Cas9-based tools. Within this scope,  to my mind the the appropriate question for assessing cancer genomics is how have these vast sums informed cancer biology?

The first is that finding "more of the same" is itself a finding; cancer genomics has used now thousands of clinical samples to validate those other findings.  This was hardly a foregone conclusion (though many had been validated on smaller scales).  Indeed, given that very few human cancers are actually caused by retroviruses, it is somewhat remarkable that the findings from retroviruses have proven so systematically enlightening in cancer.  Looking at many, many samples has also helped sort out the degree to which cancer cell line studies are valuable; remember that the most widely used cell line, HeLa, among its many issues with this line is that it represents a rare mode of tumorigenesis across the body.  Herpesvirus Human papilloma infections are a key mode of cervical cancer, oral cancers and a Burkitt's Lymphoma, but haven't been conclusively assigned to much else.

But that "more of the same" throwaway buries a lot of nuance.  One of these is the degree to which cancer genomics has refined those early observations.  For example, there are three homologs of the RAS oncogene found by retroviral work.  It is clear from studies of the genome that these are not equally troublesome genes: KRAS is mutated in very large numbers of solid tumors, NRAS in a select few types and HRAS only very rarely.  Of course, that trio could have been mapped out less expensively, but not by as much as you might think.  Much of the cost of sequencing tumors is not in the sequencing, but in the collection and assessment of the samples.

The "more of the same" slur is also lazy in that it fails to account for the fact that cancer genomics has, as suggested above, assigned the degree of involvement of different oncogenes and tumor suppressors in different tumor types.  As noted above, not every tumor has a mutated RAS, and there are some tumor types dominated by other mutated genes.  Indeed, in a number of low incidence tumors specific mutations essentially define the disease, such as hairy cell leukemia (BRAF) and  ovarian granulosa cell tumors (FOXL2).

"More of the same" also fails to account for important details filled in.  For example, protein kinases emerged as an important foci for cancer research long before genomics came into play.  The ABL half of the notorious Philadelphia Chromosome rearrangement in CML is a kinase, discovered via the retroviral route.  Other important oncogenic kinases found via retroviruses include Src, ERBB2/HER2 ERBB1/EGFR -- and the latter two are among the few retroviral oncogenes which have proven to be successful drug targets.   But there are over 500 protein kinases encoded in the human genome, and not all showed up in retroviral screens or from cell cycle studies or similar.  However, a number of these have shown up in various cancers -- but again, not every kinase is mutated in every cancer and sometimes kinases are activated by amplification rather than mutation.  Cancer genomes have helped mark some lesser-known kinases as bad actors in certain tumor types (particularly non-small cell lung cancer aka NSCLC), which in turn offers the opportunity to develop small molecule drugs.

Cancer genomics has also been valuable at identifying lineage-specific transcription factors that are important players in oncogenesis, such as ETS-related genes (ERGs) in prostate cancer and Nkx2.1 in NSCLC, and PAX8 in ovarian cancer, as well as the before mentioned FOXL2 in ovarian granulosa cell tumors.  Some of these stories are quite complex: Nkx2.1 appears to encourage lung tumor formation but discourage metastasis. Lineage specific transcription factor derangement did not originate in genomics, but tumor genomes have shown it to be recurrent pattern in a number of tumor types -- but not in many others.

Sometimes There is An Awful Lot More of the Same

A very specific example where the More of the Same catchphrase comes up grossly short can be found in the space of lymphoid malignancies and the NFκB and B-cell Receptor (BCR) pathways.  An enormous body of non-genomics work worked out these pathways (the NFκB interactome hairballs below are from that paper) and identified their relevance to immune cell function.  These works also identified scores of proteins which participated in these pathways.  Positing that some of these genes might be recurrently mutated in leukemias and lymphomas would require little imagination -- but it would take at least a mini-exome project to screen them all. Genomics on tumors has revealed that very specific genes are mutated in very specific tumors, as reviewed by Staudt.

Not Even Remotely More of the Same

Genome sequencing has revealed other classes of oncogenic mutations or processes which had not fallen out of other studies.  G-alpha signalling would be one example, with mutations in GNAQ responsible for many uveal melanomas, which originate in the eye.  Such a mutation may be responsible for the imminent silencing of the eloquent Oliver Sacks.  While there was certainly evidence from other approaches that epigenetic reading and writing might play a role in tumors, this was nailed down by finding recurrent mutations in the enzymes for reading and writing epigenetic marks. The involvement of specific, recurrent mutations in a splicing factor (U2AF1) has been observed in both myelodysplastic syndromes and lung adenocarcinomas and an RNA-binding protein in lung adenocarcinomas.

Perhaps the most amazing story started with the discovery of mutations in the Krebs cycle enzyme isocitrate dehydrogenase (IDH) in certain hematologic tumors. These were originally thought to be loss-of-function changes, with the ensuing puzzle of how meddling with the Krebs cycle -- and only that one step -- might benefit a tumor.  The answer came from the stunning discovery that these are actually neopmorphic mutations which endow the enzyme with a shift in biochemical activity, generating a novel metabolite which in turn inhibits another cellular enzyme which affects epigenetics, ultimately resulting in a failure in developmental progression.  Another company funded by the same venture firm that started my company has a compound in clinical development targeting this abnormal activity; in early trials it appears to be a remarkably effective drug that encourages the rogue cells to fully differentiate (disclosure: I briefly consulted for Agios in 2009, though I have never held any equity in the company).

Even farther from resemblance to "more of the same" are learnings around mutation processes, such as discovering in the first lung tumor whole genome sequence a mutation pattern unassignable to previously known mutation modes.  More recently, a specific lesion in a DNA polymerase has been found to lead to a distinct mutational profile as well as a clinically relevant subtype of gliomas.

Playing "What If" is fun, but arguing over alternative histories ultimately is a pointless exercise in personal biases, as there is no way to falsify one unreal version of events from a different.  But I will throw out this to ponder: if whole genome sequencing had been invented sooner, it would easily have rediscovered virtually all of the classically identified oncogenes, either by looking for recurrent mutations or amplifications.

Perhaps what cancer genomics approaches are uniquely suited for understanding is the clonal complexity of tumors and the progression of such complexity over time

For Patients, This All Matters

Just adding knowledge of the human body to the body of human knowledge with  is always rewarding, but the claim of cancer genomics is that it would have immediate and lasting impact on clinical practice.  Has this been the case?  I think there are a number of trends which can be pointed to.  First, companies such as Foundation Medicine and several large cancer centers have launched broad somatic mutation testing programs relying on the technologies developed in the cancer genome projects. These have been reported to identify actionable mutations in well over half of samples.  Now, it is important not to confuse actionable, which suggests one or more lines of therapy to consider or avoid, with effective.  The complex clinical studies to prove such efficacy are underway, but will probably also be a constantly moving target.

The genes indicated as mutated by cancer genomics have been, as one might expect, a grab-bag of the druggable and undruggable, But the druggable set has launched a number of companies and driven a number of genomics-focused trials.  I've touched on Agios above; another company in the space is Blueprint Medicines (another company funded by our VCs & our landlord for the first year of laboratory operations).  Upstairs from us is a company in the cancer epigenetics space, some of whose trials are based around mutations found via cancer genomics. Foundation Medicine and its competitors are running tens of thousands of tests to search patient genomes for mutations in order to inform their therapy. So cancer genomics is having an important impact on the drug discovery and clinical scene.

The impact of cancer genomics has not been equally felt across cancer types.  Numerous insights, many suggesting therapeutic routes, have been found for lung cancers.  In prostate, fusions with the gene ERG have turned out to be common.  Ovarian cancer seems to frequently have actionable mutations.  On the other hand, my impression is that breast cancer has been frustratingly refractive to this approach.  Further subdivision  of breast cancer into broad classes that have interesting biology, yes, but actual radical changes in diagnosis or therapy, not really.  There is an approved test to stratify breast cancer, but there is little evidence it is setting the oncology world on fire.  Similarly, while many useful findings have been found for other major solid tumor types, quite a few tumors seem to be singletons in terms of their mutations.

What Next ?

It's my understanding that early this year TCGA came to a natural conclusion (despite much effort, I can't find the article I thought I saw).  Even if that isn't quite right, the initial plan was to sequence hundreds of samples for specified tumor types.  Some of the proponents of cancer genomics suggest that for the big tumor types where cancer genomics hasn't had big payouts, the correct response is to double down and sequence thousands or tens of thousands of tumors.  Despite my rousing defense above of what has been done to date, I'm decidedly ambivalent about a further big bet in this space, for a number of reasons.

First, it may not be necessary, or at least a very different approach towards the same end might make sense.  With increasing use of large gene panels in routine cancer patient care, perhaps what needs funding is informational infrastructure that ensures that all that information, with appropriate clinical metadata, is captured for later analysis (while preserving appropriate privacy safeguards).  Developing robust systems to capture this information from clinical practice will require significant effort; the penalty for not developing such systems will be parallel but separate programs of research and clinical mutation discovery.

Another thought is that perhaps such a blunderbuss approach is just too much for too high a risk.  In its place, one could continue to sequence very specific, pathologically-defined tumor subtypes. This would continue the thought that many rare cancers act as almost monogenic diseases. Unusual subtypes of common tumors can have similar properties.  For example, the signet ring subtype of lung adenocarcinoma corresponds very well with EML4-ALK fusions; presumably the fusion protein triggers some specific developmental programs which are not triggered in such cancers driven by other oncogenes.  My friend's tumor is a signet ring subtype of colorectal cancer; perhaps it also has a distinctive driver gene.  There is now a suggestion of a common genomic pattern to the dreaded triple negative breast cancers.  

A second reservation is perhaps the funds would be better spent on following up the findings from the first round of the project.  Working out the biology of all those identified mutations would likely advance the field of cancer biology (and probably biology in general) greatly.

A final reservation is that perhaps the world of cancer therapy has truly undergone a seismic shift, and further public efforts need to recognize that shift.  The shift is the astonishing run of success for immunotherapies.  While it would be foolish to think that these new treatments have won the war on cancer, they have certainly radically altered the landscape.  Genomics may play a role here too -- there is already one report of overall mutational burden being positively correlated with immunotherapy response in non-small cell lung cancer.

Genomics has contributed greatly to our understanding of the biology of cancer and is already making inroads on changing the treatment of cancer.  To deny this is to make a claim divorced from reality.  However, reality also demands that the balance of research resources in cancer be constantly re-evaluated.