Showing posts with label genomewide association studies. Show all posts
Showing posts with label genomewide association studies. Show all posts

Thursday, July 29, 2010

GWAS advertising legerdemain

There's a recent GWAS review by Teri Manolio in the New England Journal of Medicine that demands a response, even in just our little blog. Dr Manolio reviews the success and (some of) the less positive issues attending to the genetic approach to disease.

This article lays out the nature, and the positive findings, of genomewide association studies. Manolio says things like:
Genomewide association studies — in which hundreds of thousands of single-nucleotide polymorphisms (SNPs) are tested for association with a disease in hundreds or thousands of persons — have revolutionized the search for genetic influences on complex traits.
And
Genomewide association studies have proved successful in identifying genetic associations with complex traits.
But she demurs from citing a number of authors who have raised substantial points critical of the GWAS approach, though the supportive literature is of course well represented.

The problem is that Dr Manolio is a bureaucrat working for the NIH's Human Genome Research Institute. She is a skilled person, but her job is advocacy of a particular program agenda--the funding of genetic research--and hence she has a vested interest in promoting the work they've decided to fund and hence advertising it as a success. Perhaps that's in her 'job description'--to be an advocate for a policy she feels is a good one. But that shouldn't be confused with science.

If the NEJM were ethically responsible (there have been many issues about that in recent years, including their relationship to the evaluation of drug safety and drug trial data), it would not publish an article evaluating GWAS written by a person vested in advancing that type of study. Such a review must be viewed as essentially a conflict of interest. And given the same suspicion that drug trials sponsored by drug companies get and have richly deserved.

It is not that GWAS are all bad or a total waste of resources. But they are far from as good as the article says. We've made many posts about GWAS and need not repeat them here (interested readers can find them by searching the blog). But a cheer-leading article in a prominent journal like the NEJM can and probably will be seen as evidence for the success of the effort to turn complex traits into genetic traits.

One legitimate issue, of course, is that investment in one place diverts funds from other avenues of research. There are areas in which the same investment might have much greater, and more immediate returns in terms of actual health improvement, even if such measures aren't as glamorous for the research industry.

And there's a further problem. Publishing this propaganda piece in the NEJM implies that GWAS have clinical relevance and are about 'medicine'. In a few rare cases (naturally, they're featured in the article) this is partly true, though the role of GWAS in their primary discovery is less clear. But generally we are so far from being able to apply GWAS in clinical practice that a review of GWAS results should not appear in a medical journal.

There are some new approaches being taken in association mapping, including those that go beyond considering just the most statistically 'significant' genome regions found for a given disease. They try to digest the information about risk from all or at least many more of the tested markers along the genome. These approaches are briefly mentioned in the article, but Dr Monolio does not say that by and large GWAS lead only to general statements of risk that have very little specific genetic value since most of the implicated regions contribute trivially to risk on their own.

And the article is naive about (and/or intentionally fails to cite) other problems, aspects related to evolution, and is downright misleading about the history of 'theory' in this area, which is much more a history of advocacy than of science.

The article provides a good summary about what GWAS are, with nice figures to show this. But it must be read as lobbying. It's too bad we have to live in an era when this is the way things are done. Science could make better progress, and contribute more directly to taxpayers who support it, if decisions about it were more centered in science itself.

Saturday, May 23, 2009

Genetic leaf-litter

There are many ways in which everyone is a conceptual prisoner, encaged in culturally based limits. We are born to, and trained in and entrained by our circumstances, and these in turn are a legacy of history. We can try to escape from this but probably the most we can hope for is to keep subtle assumptions and constraints at bay. In genetics, there is a pervasive concept of the 'wild type', a concept that goes back into the history of genetic research, referring to the natural allele at a gene, that was favored by a history of selection, relative to which other alleles (mutational variants) were viewed as generally rare and harmful (waiting to be shortly removed by natural selection).

There is a tacit extension of this gene-specific concept to the whole genome (or even organism) as when 'normal' inbred laboratory mice are referred to as the 'wild type' relative to an experimental modification such as a transgenic gene knockout mouse of the same strain.
Sometimes this is clear shorthand, but beware of conceptual shorthand! An implication of this kind of genetic thinking is that in regard to human traits, including especially disease, there is the normal human genome as represented by 'the' human genome sequence available in genome data bases, and the disease-causing mutants. But in fact genomes are very large sequences of DNA that serve as targets for mutation in every cell, every individual, every generation.

We know that biological traits are the result of developmental processes that include countless genes (of the classical protein-coding type as well as many other functional DNA sequence elements). Species contain large numbers of members--there are about 7
billion of us humans stalking the Earth. What this means is that there is a potentially huge amount of variation at most if not all viable spots in our genome. After a mutation occurs, it may proliferate if its bearer successfully reproduces. Over time, some of these alleles grow in frequency to become quite common.

When genomic DNA is sequenced in a number of individuals, this variation is easily detected. But whether affected by natural selection or just by the chance aspects of reproductive success or failure, most allelic variation that is present in genomes at any given time is rare. Relative to the more common variants, this genetic variation is a kind of leaf-litter of variation. Even with hundreds of thousands or, indeed, hundreds of millions of very rare variants present in our species, any small sample will pick up some of them by chance.

In a small sample, those will seem
to be more common than they are; so if we sequenced 5 people (10 copies of the genome) the lucky variants whose true population frequency is only a few in a billion that by chance are in the 5 people we sample, will seem to have a frequency of at least 10% (one copy of the 10 we sampled being the variant). The tip-off that this genomic leaf-litter exists is that most of the variants are not seen in other samples, or if common enough to be sampled more than once, usually only seen in samples from the same geographic region (because that's where they arose as new mutations, and were transmitted to descendants who remained living in the same continent). In developed countries, variants that cause disease will show up in specialty clinics at major medical centers.

In trying to find variants by mapping, as in genomewide association studies (GWAS) that compare sequences between cases and controls, we may feel that we have so far detected the common, but not all the rare causal variants that exist. But we may also feel that if we can just enlarge our samples, we'll get a much better handle on the nature of the effects of these variants, or we'll detect the remaining variants that haven't yet been detected.


This is likely to be an illusion, as the growing number of those of us who argue that very large GWAS will not bring a big payoff of the kind envisioned and promised by those who argue for this kind of project. There are several reasons for this skepticism.
First, it is hard to detect rare things with statistical significance, much less to get a good idea of their effects and action. One needs huge samples to get enough instances to show that the variant is meaningfully more common in cases than controls.

But second, the leaf-litter phenomenon means that as sample sizes increase, more and more rarer and rarer variants will be picked up. It will be difficult to show clearly that they are causally involved with our trait, but even if they are they will have less and less effect on public health. They will vary from population to population, and sample to sample from the same population. Environments may affect whether carriers of the variant manifest the disease, and most such variation will at most have minor effect on risk of disease (if the effect were stronger, the allele would have been removed by selection, or we would have been able to detect it in family studies).

And if it requires more than one such variant, or even many of them, to combine to produce disease, the detection and evaluation situation will be that much more challenging, if not pointless.
There will always be exceptions, as is true about the nature of life. But the leaf-litter phenomenon is real and there is plenty of evidence for it. It is predicted by population genetics theory. And it is consistent with results of mapping studies that have been done to date. Ironically, perhaps, while the individual rare alleles have little detectable effects, their aggregate effects in the population may account for the observed heritability (familial aggregation of risk, or similarity of trait values) of most traits, including disease. That heritability, which is clearly there, is what has been considered mysterious given the failure of linkage or GWAS studies to find the genes that are responsible.

We are presented with a kind of epistemological paradox: the genetic variation exists, but we may have insurmountable challenges to find most of it. Indeed, it is somewhat mystical even to argue that it exists as individual effects, if they cannot be found or replicated by current statistical genetic methods.
Evolution 'cares' about reproductive success, not about simplicity in genetic causation. From a population perspective, evolution occurs because mutations occur generating variation that selection and chance can effect from one generation to the next.

Genetic leaf-litter is thus the fuel for evolution. We may care to know the cause of each instance of a trait or disease, but Nature has only cared about viability and success, and tolerates the leaf-litter. As massive amounts of human DNA sequence are produced, we will see this. It will be an incredible playground for population and evolutionary geneticists. But what we do with it, in terms of identifying disease causation, is not clear.

Tuesday, April 21, 2009

GWAS revisited: vanishing returns at expanding costs?

We've now had a chance to read the 4 papers on genomewide association studies (GWAS) in the New England Journal of Medicine last week, and we'd like to make a few additional comments. Basically, we think the impression left by the science commentary in the New York Times that GWAS are being seriously questioned by heretofore strong adherents was misleading. Yes, the authors do suggest that all the answers are not in yet, but they are still believers in the genetic approach to common, complex disease.

David Goldstein (whose paper can be found here) makes the point that SNPs (single nucleotide polymorphisms, or genetic variants) with major disease effects have probably been found by now, and it's true that they don't explain much of the heritability (evidence of overall inherited risk) of most diseases or traits. He believes that further discoveries using GWAS will generally be of very minor effects. He concludes that GWAS have been very successful in detecting the most common variants, but now have reached the point of diminishing returns. He says that "rarer variants will explain missing heritability", and these can't be identified by GWAS, so human genetics now needs to turn to sequencing whole genomes to find these.

Joel Hirschhorn (you can find his paper here) states that the main goal of GWAS has never been disease prediction, which indeed they've only had modest success with, but rather the discovery of biologic pathways underlying polygenic disease or traits. GWAS have been very successful at this--that is, they've confirmed that drugs already in use are, as was basically also known, targeting pathways that are indeed related to the relevant disease, although he says that further discoveries are underway. Unlike Goldstein, he believes that larger GWAS will find significant rare variants associated with disease.

Peter Kraft and David Hunter (here) tout the "wave of discoveries" that have resulted from GWAS. They do say that by and large these discoveries have low discriminatory ability and predictive power, but believe that further studies of the same type (only much bigger) will find additional risk loci that will help explain polygenic disease and yield good estimates of risk. They suggest that, because of findings from GWAS, physicians will be able to predict individual risk for their patients in 2 to 3 years.

John Hardy and Andrew Singleton (here) describe the GWAS method and point out that people are surprised to learn that it's often just chromosome regions that this method finds, not specific genes, and that some of these are probably not protein-coding regions but rather have to do with regulating gene expression. Notably, unlike the other authors who all state that the "skeptics were wrong", but somehow don't bother to cite their work so that the reader could check that claim (they do cite the Terwilliger and Hiekkalinna paper we mentioned here last week, but that is on a specialized technical issue, not the basic issues related to health effects).

They also state that the idea of gene by environment interaction is a cliche, and has never been demonstrated. Whether they mean by this that there is no environmental effect on risk or simply that it's difficult to quantify (or, a technical point, that environmental effects are additive) is not clear. If the former, that's patently false--even risk of breast cancer in women who do carry the known and undoubted BRCA1 or BRCA2 risk alleles, varies significantly by decade of birth. Or the huge rise in diabetes, obesity, asthma, autism, ADHD, various cancers, and many other diseases just during the memory of at least some living scientists who care to pay attention. And, see our post of 4/18.

So, we find none of the supposed general skepticism here. Yes, these papers do acknowledge that risk explained by GWAS has been low, but they claim this as 'victory' for the method, and dismiss, minimize, or (worse) misrepresent problems that were raised long ago, and instead say either that risk will be explained with bigger studies, or GWAS weren't meant to explain risk in the first place (it's not clear that the non-skeptics agree with each other about the aim of GWAS, or about whether they have now served their purpose and it's time to move on--to methods that apparently actually do or also do explain heritability and predict risk.)

The 'skeptics' never said that GWAS would find nothing. What at least some of us said was that what would be found would be some risk factors, but that complex traits could not by and large be dissected into the set of their genetic causes in this way.

Rather than face these realities, we feel that what is being done now is to turn defeat into victory by claiming that ever-larger efforts will finally solve the problem. We think that is mythical. Unstable and hardly-estimable small, probabilistic relative risks will not lead to revolutionary 'personalized medicine', and there are other and better ways to find pathways. If a pathway (network of interacting genes) is so important, it should have at least some alleles that are common and major enough that they should already be known (or could easily be known from, say, mouse experiments); once one member is known, experimental methods exist to find its interacting gene partners.

In a way it's also a sad consequence of ethnocentric thinking to suppose that because we can't find major risk alleles in mainstream samples from industrialized populations, that such undiscovered alleles might not exist in, or even be largely confined to, smaller or more isolated populations, where they could be quite important to public health. They do and, ironically, mapping methods (a technical point: especially linkage mapping) can be a good way to find them.

But if we're in an era of diminishing, if not vanishing, returns, we're also in an era in which we think we will not only get less, but will have to spend and hence sequester much more research resources to get it. So there are societal as well as scientific issues at stake.

In any case, we already have strong, pathway-based personalized medicine! By far the major risk factor for most diabetes, for example, involves energy and fat metabolic pathways. Individuals at risk can already target those pathways in simple, direct ways: walk rather than taking the elevator, and don't over-eat!

If those pathways were addressed in this way, there would actually be major public impact, and ironically, what would remain would be a residuum of cases that really are genetic in the meaningful sense, and they would be more isolated and easier to study in appropriate genetic, genomic, and experimental ways.

Saturday, April 18, 2009

The rear-view mirror and the road ahead

We've already posted some critiques of the current push for ever-larger genomewide association-style studies of disease (GWAS) which have been promoted by glowing promises that huge-scale studies and technology will revolutionize medicine and cure all the known ills of humankind (a slight exaggeration on our part, but not that far off the spin!). We want to explain our reasoning a bit more.

For many understandable reasons, geneticists would love to lock up huge amounts of research grant resources, for huge amounts of time, to generate huge amounts of data that will be deliciously interesting to play with. But such vast up-front cost commitments may not be the best way to eliminate the ills of humankind. It may not even be the best way to understand the genetic involvement in those ills.

In a recent post we cited a number of our own papers in which we've been pointing out problems in this area for many years, and while we didn't give references we did note that a few others have recently been saying something like this, too. The problem is that searching for genetic differences that may cause disease is based on designs such as comparing cases and controls, which don't work very well for common, complex diseases like diabetes or cancers. Among other reasons this is because, if the genetic variant is common, people without the disease, the controls, may still carry a variant that contributes to risk, but they might remain disease-free because, say, they haven't been exposed to whatever provocative environment is also associated with risk (diet, lack of exercise, etc.). And these designs don't work very well for explaining normal variation.

As we have said, the knowledge of why we find as little as we are finding has been around for nearly a century, and it connects us to what we know about evolutionary genetics. Since the facts apply as well to almost any species--even plants, inbred laboratory mice, and single-celled species like yeast--they must be telling us something about life that we need to listen to!

Part of the problem is that environments interact with many different genes to produce the phenotypes (traits, including disease) in ways that would be good to understand. However, our methods of understanding causation necessarily look backwards in time (they are 'retrospective'): we study people who have some trait, like diabetes, and compare them to age-sex-etc. matched controls, to see how they differ. Geneticists and environmental epidemiologists stress their particular kinds of risks, but the trend recently has strongly been to focus on genes, partly because environmental risk factors have proven to be devilishly hard to figure out, and genetics has more glamour (and plush funding) these days: it may have the sexy appearance of real science, since it's molecular!

Like looking in the rear-view mirror, we see the road of risk-factor exposures that we have already traveled. But what we really want to understand is the causal process itself, and for 'personalized medicine' and even public health we need to look forward in time, to current people's futures. That is what we are promising to predict, so we can avoid all ills (and produce perfect children).

We need to look at the road ahead, and what we see in the rear-view mirror may not be all that helpful. We know that the environmental component of most common diseases contributes far more to risk than any specific genetic factors, probably far more than all genetic factors combined do on their own. We know that clearly from the fact that many if not most common diseases have changed, often dramatically, in prevalence just in the last couple of generations, while we've had very good data and an army of investigators tracking exposures, lifestyles, and outcomes.

Those changes in prevalence are a warning shot across the genetics bow that geneticists have had a very convenient tin ear to. They rationalize these clear facts by asserting that changes in common diseases are due to interactions between susceptible genotypes and these environmental changes. Even if such unsupported assertions were true, what we see in the rear-view mirror does not tell us what the road ahead will be like, for the very simple, but important reason that there is absolutely no way to know what the environmental--the non-genetic--risk factor exposures will be.

No amount of Biobanking will change this, or make genotype-based risk prediction accurate (except for the small subset of diseases that really are genetic), because each future is a new road and risks are inevitably assessed retrospectively. Even if causation were relatively simple and clear, which is manifestly not the case. No matter how accurately we can identify the genotypes of everyone involved (and there are some problems there, too that we will have to discuss another time).

This is a deep problem in the nature of knowledge in regard to problems such as this. It is one sober, not far-out, not anti-scientific, reason why scientists and public funders should be very circumspect before committing major amounts of funding, for decades into the future, to try to track everyone, and everyone's DNA sequences. And here we don't consider the great potential for intrusiveness that such data will enable.

As geneticists, we would be highly interested in poking around in the data mega-studies would yield. But we think it would not be societally responsible data to generate, given the other needs and priorities (some of which actually are genetic), that we know we can address with available resources and on other problems or approaches.

We can learn things by checking the rear-view mirror, but life depends on keeping our eye on the road ahead.

Thursday, April 16, 2009

GWAS: really, should anyone be surprised?

There's a story today in the New York Times about papers just published in the New England Journal of Medicine (embargoed for 6 months, so we can't link to it here) questioning the value of GWAS--genomewide association studies. We're interested because we, but largely Ken, often in collaboration with Joe Terwilliger at Columbia, have been writing for many years--in many explicit ways and for what we think are the right reasons, for 20 years or more--about why most common diseases won't have simple single gene, or even few gene explanations.

"The genetic analysis of common disease is turning out to be a lot more complex than expected," the reporter writes. Further, "...the kind of genetic variation [GWAS detect] has turned out to explain surprisingly little of the genetic links to most diseases." Of course, it depends on who's expectations you're talking about, and who you're trying to surprise. It may be a surprise for a genetics true-believer, but not for those who have been paying attention to the nature of genomic causation and how it evolved to be as it is (the critical facts and ideas have been known, basically, since the first papers in modern human genetics more than 100 years ago).

GWAS are the latest darling of the genetics community. Meant to identify common genetic factors that influence disease risk, the method scans the entire genome of people with and without the disease to look for genetic variants associated with disease risk. Many papers have been published claiming great success with this approach, and proclaiming that finally we're about to crack disease genetics and the age of personalized medicine is here. But upon scrutiny these successes turn out not to explain very much risk at all--often as little as 1%, 3% (even if the relative risk is, say 1.3--a 30% increase, or in a few cases 3.0 or more--there will always be excpetions). And this is for reasons that have been entirely predictable, based on what is known about evolution and genes.

Briefly, genes with major detrimental effects by and large are weeded out quickly by natural selection, most traits, including disease, except for the frankly single-gene diseases (which can stay around because they're partly recessive), are the result of many interacting genes, and, particularly for diseases with a late age of onset, environmental effects. And, there are many genetic pathways to any trait, so that the assumption that everyone with a given disease gets there the same way has always been wrong. Each genome is unique, with different, and perhaps rare or very rare genes contributing to disease risk and these will be difficult or impossible to find with current methods. Risk alleles can vary between populations, too--different genes are likely to contribute to diabetes in, say, Finns than in the Navajo. Or even the French. Or even different members of the same family! Inconvenient truths.

Now, news stories and even journal articles rarely point out any of these caveats. Indeed, David Goldstein is cited in the Times story as saying that the answer is individual whole genome sequencing, another very expensive and still deterministic approach (that surely will now be contorted by the proponents of big Biobanks to show that this is just the thing they've had in mind all along!). Nobody backs away from big long-term money just to satisfy what the science actually tells us. Now maybe there is the story, in the public interest, that a journalist ought to take on.

So, the push will be for ever-more complete DNA sequences to play with, but this is not in the public interest in the sense that it will not have major public health impact. Even if it identifies new pathways, one of the major rationales given in the face of the awkward epidemiological facts, which is unlikely to be a major outcome in public health terms. We have many ways to identify pathways, and more are becoming available all the time. While whole sequences can identify unique rare haplotypes or polygenotypes that some affected people share, that is really little more than trying the same method on new data, like Cinderella's wicked step-sisters forcing their feet into the glass slipper.

If it's true as it seems to be, that most instances of a disease are due to individually rare polygenotypes, then the foot will not fit be any better than before. And it won't get around the relative vs absolute risk, nor the environmental, nor the restrospective/prospective epistemiological problem. These are serious issues, but we'll have to deal with them separately. And the rarer the genotype the harder to show how often it is found in controls, hence the harder to estimate its effect.

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A few reasons why no one should be surprised:

*Update* Here are a few of the papers that have made these points in various ways and contexts over the years. They have references to other authors who have recently made some of these points. The point (besides vanity) is that we are not opportunistically jumping on a new bandwagon, now that more people are (more openly) recognizing the situation. In fact, the underlying facts and reasons have been known for even a far longer time.

The basic facts and theory were laid out early in the 20th century by some of the leaders of genetics, including RA Fisher, TH Morgan, Sewall Wright, and others.

Kenneth Weiss, Genetic Variation and Human Disease, Cambridge University Press, 1993.

Joseph Terwilliger, Kenneth Weiss, Current Opinion in Biotechnology, 9(6), 578-594 (1998). Linkage disequilibrium mapping of complex disease: fantasy or reality?

Kenneth Weiss, Joseph Terwilliger, Nature Genetics 26, 151 - 157 (2000). How many diseases does it take to map a gene with SNPs?

Joseph Terwilliger, Kenneth Weiss, Annals of Medicine 35: 532-544 (2003). Confounding, ascertainment bias, and the quest for a genetic "Fountain of Youth".

Kenneth Weiss, Anne Buchanan, Genetics and the Logic of Evolution, Wiley, 2004.

Joseph Terwilliger, Tero Hiekkalinna, European Journal of Human Genetics, 14, 426–437 (2006). An utter refutation of the 'Fundamental Theorem of the HapMap'.

Anne Buchanan, Kenneth Weiss, Stephanie M Fullerton, International Journal of Epidemiology, 35(3):562-571 (2006). Dissecting complex disease: the quest for the Philosopher's Stone?

Kenneth Weiss, Genetics 179, 1741–1756 (2008). Tilting at Quixotic Trait Loci (QTL): An Evolutionary Perspective on Genetic Causation.

Anne Buchanan, Sam Sholtis, Joan Richtsmeier, Kenneth Weiss, BioEssays, What are genes for or where are traits from? What is the question? BioEssays 31:198-208 (2009).