Obesity is one of our more widespread and serious health-threatening traits. Many large-scale mapping as well as extensive environmental/behavioral epidemiological studies of obesity have been done over recent decades. But if anything, the obesity epidemic seems to be getting worse.
There's deep meaning in that last sentence: the prevalence of obesity is
changing rapidly. This is being documented globally, and happening rapidly before our eyes. Perhaps the most obvious implication is that this serious problem is
not due to genetics! That is, it is
not due to genotypes that in themselves make you obese. Although everyone's genotype is different, the changes are happening during lifetimes, so we can't attribute it to the different details of each generation's genotypes or their evolution over time. Instead, the trend is clearly due to lifestyle changes
during lifetimes.
Of course, if you see everything through gene-colored lenses, you might argue (as people have) that sure, it's lifestyles, but only some key nutrient-responding genes are responsible for the surge in obesity. These are the 'druggable' targets that we ought to be finding, and it should be rather easy since the change is so rapid that the genes must be few, so that even if we can't rein in McD and KFC toxicity, or passive TV-addiction, we can at least
medicate the result. That was always, at best, wishful thinking, and at worst, rationalization for funding Big Data studies. Such a simple explanation would be good for KFC, and an income flood for BigPharma, the GWAS industry, DNA sequencer makers, and more.....except not so good for those paying the medical price, and those who are trying to think about the problem in a disinterested scientific way. Unfortunately, even when it is entirely sincere, that convenient hope for a simple genetic cause is being shown to be false.
A serious parody?Year by year, more factors are identified that, by statistical association at least and sometimes by experimental testing, contribute to obesity. A very fine
review of this subject has appeared in the mid-October 201
Nature Reviews Genetics, by Ghosh and Bouchard, which takes seriously not just genetics but all the plausible causes of obesity, including behavior and environment, and their relationships as best we know them, and outlines the current state of knowledge.
Ghosh and Bouchard provide a well-caveated assessment of these various threads of evidence now in hand, and though they do end up with the
pro forma plea for yet more funding to identify yet more details, they provide a clear picture that a serious reader can take seriously on its own merits. However, we think that the proper message is
not the usual one. It is that we need to rethink what we've been investing so heavily on.
To their great credit, the authors melded behavioral, environmental, and genetic causation in their analysis. This is shown in this figure, from their summary; it is probably the best current causal map of obesity based on the studies the authors included in their analysis:
If this diagram were being discussed by John Cleese on Monty Python, we'd roar with laughter at what was an obvious parody of science. But nobody's laughing and this isn't a parody! And it is by no means of unusual shape and complexity. Diagrams like this (but with little if any environmental component) have been produced by analyzing gene expression patterns even just of the early development of the simple sea urchin. But we seem not to be laughing, which is understandable because they're serious diagrams. On the other hand, we don't seem to be reacting other than by saying we need more of the same. I think that is rather weird, for scientists, whose job it is to understand, not just list, the nature of Nature.
We said at the outset of this post that 'the obesity epidemic seems to be getting worse'. There's a deep message there, but one essentially missing even from this careful obesity paper: it is that many of the causal factors, including genetic variants, are changing before our eyes. The frequency of genetic variants changes from population to population and generation to generation, so that all samples will look different. And, mutations happen in every meiosis, adding new variants to a population every time a baby is born. The results of many studies, as reflected in the current summary by Ghosh and Bouchard, show the many gene regions that contribute to obesity, their total net contribution is still minor. It is possible, though perhaps very difficult to demonstrate, that an individual site might account more than minimally for some
individual carriers in ways GWAS results can't really identify. And the authors do cite published opinions that claim a higher efficacy of GWAS relative to obesity than we think is seriously defensible; but even if we're wrong, causation is very complex as the figure shows.
The individual genomic variants will vary in their presence or absence or frequency or average effect among studies, not to mention populations. In addition, most contributing genetic variants are too rare or weak to be detected by the methods used in mapping studies, because of the constraints on statistical significance criteria, which is why so much of the trait's heritability in GWAS is typically unaccounted for by mapping. These aspects and their details will differ greatly among samples and studies.
Relevant risk factors will come or go or change in exposure levels in the future--but these cannot be predicted,
not even in principle. Their interactions and contributions are also manifestly context-specific, as secular trends clearly show. Even with the set of known genetic variants and other contributing factors, there are essentially an unmanageable number of possible combinations, so that each person is genetically and environmentally unique, and the complex combinations of future individuals are not predictable.
Risk assessment is essentially based on replicability, which in a sense is why statistical testing can be used (on which these sorts of results heavily rely). However, because these risk factor combinations are each unique they're not replicable. At best, as some advocate, the individual effects are additive so that if we just measure each in some individual add up each factor's effect, and predict the person's obesity (if the effects are not additive, this won't work). We can probably predict, if perhaps not control, at least some of the major risk factors (people will still down pizzas or fried chicken while sitting in front of a TV). But even the known genetic factors in total only account for a small percentage of the trait's variance (the authors' Table 2), though the paper cites more optimistic authors.
The result of these indisputable facts is that as long as our eyes are focused, for research strategic reasons or lack of better ideas, on the litter of countless minor factors, even those we
can identify, we have a fat chance of really addressing the problem this way.
If you pick any of the arrows (links) in this diagram, you can ask how strong or necessary that link is, how much it may vary among samples or depend on the European nature of the data used here, or to what extent even its identification could be a sampling or statistical artifact. Links like 'smoking' or 'medication', not to mention specific genes, even if they're wholly correct, surely have quantitative effects that vary among people even within the sample, and the effect sizes probably often have very large variance. Many exposures are notoriously inaccurately reported or measured, or change in unmeasured ways. Some are quite vague, like 'lifestyle', 'eating behavior', and many others--both hard to define and hard to assess with knowable precision, much less predictability. Whether their various many effects are additive or have more complex interaction is another issue, and the connectivity diagram may be tentative in many places. Maybe--probably?--in such traits simple behavioral changes would over-ride most of these behavioral factors, leaving those persons for whom obesity really is due to their genotype, which would then be amenable to gene-focused approaches.
If this is a friable diagram, that is, if the items, strengths, connections and so on are highly changeable, even if through no fault of the authors whatever, we can ask when and where and how this complex map is actually useful, no matter how carefully it was assembled. Indeed, even if this is a rigidly accurate diagram
for the samples used, how applicable is it to other samples or to the future?Or how useful is it in predicting not just group patterns, but individual risk?
Our personal view is that the rather ritual plea for more and more and bigger and bigger statistical association studies is misplaced, and, in truth, a way of maintaining funding and the status quo, something we've written much about--the sociopolitical economics of science today. With obesity rising at a continuing rate and about a third of the US population recently reported as obese, we know that the future health care costs for the consequences will dwarf even the mega-scale genome mapping on which so much is currently being spent, if not largely wasted. We know how to prevent much or most obesity in behavioral terms, and we think it is entirely fair to ask why we still pour resources into genetic mapping of this particular problem.
There are many papers on other complex traits that might seem to be simple like stature and blood pressure, not to mention more mysterious ones like schizophrenia or intelligence, in which hundreds of genomewide sites are implicated, strewn across the genome. Different studies find different sites, and in most cases most of the heritability is not accounted for, meaning that many more sites are at work (and this doesn't include environmental effects). In many instances, even the trait's definition itself may be comparably vague, or may change over time. This is a landscape 'shape' in which every detail is different, within and between traits, but is found in common with complex traits. That in itself is a tipoff that there is something consistent about these landscapes but we've not yet really awakened to it or learned how to approach it.
Rather than being skeptical about these Ghosh and Bouchard's' careful analysis or their underlying findings, I think we should accept their general nature, even if the details in any given study or analysis may not individually be so rigid and replicable, and ask: OK, this
is the landscape--what do we do now?
Is there a different way to think about biological causation? If not, what is the use or point of this kind of complexity enumeration, in which every person is different and the risks for the future may not be those estimated from past data to produce figures like the one above? The rapid change in prevalence shows how unreliable these factors must be, at prediction--they are retrospective of the particular patterns of the study subjects. Since we cannot predict the strengths or even presence of these or other new factors, what should we do? How can we
rethink the problem?
These are the harder question, much harder than analyzing the data; but they are in our view the real scientific questions that need to be asked.
