Morgan's insight--and Morgan's restraint

Last week, we stirred the pot by asserting that it was at best misleading for the authors of the latest human stature mega-study to say, as if reassuringly, that the number of genome locations contributing to stature was in the thousands, but that at least it was finite. We questioned that 'finite' both figuratively and literally, because it has to do with the realities and manageability of this sort of causal landscape.  And this is for what appears to be a highly genetic and easily measured trait.

Defenders of the faith tweeted sneeringly at these points.  Our view is that current practice is largely chasing rainbows, and we know it, and we had solid century-old theoretical reasons to expect the kind of complexity that's been found (countless contributing factors to complex traits).  The essential nature of the findings was clearly predicted, before and during the large-scale mapping era. Initially, one could argue that the theory of 'polygenic' inheritance was non-specific and the growth of whole genome studies confirmed it.  That, in itself, was a major success, not a failure, though it showed that using genomes to predict complex traits is problematic.

We have said that by now we have enough actual explicit genomic evidence to show the lay of the land--predicting phenotypes from genotypes is, and will continue to be problematic.  It's long time to stop chasing these rainbows and to stop making exaggerated promises of pots of medical gold to come. Some funding groups have said as much, but the push for ever bigger is not abating.

In our post, we used a quote from TH Morgan's 1926 book, The Theory of the Gene. Morgan was a major figure who laid the linkage and mapping framework for today's finds.  He made statements about stature and its complex causal basis that have stood a century of time, and the quote we used made our point.

Of course, selective retro-quoting is as dicey as using retro-fitted data to allege predictive power.  We can mine our forebears for quotes that seem prescient....because they support our own point of view. But exegesis is a game anyone can play.  You can usually find that the same author, or his contemporaries, said  things that don't support our view.  Industries of professors have made their careers by mining history for antecedents whose quotes presaged major discoveries such as of relativity, evolution, and so on, and/or helped stimulate Einstein or Darwin.  So, quoting Morgan was a rhetorical device for making a point, and in itself the quote has no scientific heft.

In fact, however, the quote reflects Morgan's views about what he was doing--and about what science at the time was not yet equipped to do.  Wisely, perhaps more than in today's environment, he simply refrained from doing what was not yet seriously feasible.

Morgan's contributions in the famous fly room are well documented (an interesting account is in Lords of the Fly, by RE Kohler, 1994, U Chicago Press).  He had a major, clearly important agenda.  Mendel had shown evidence that (carefully selected) traits could be inherited in what appeared to be a kind of "point" causation--single transmissible causal factors.  Mendel worked in the context of the newly developing atomic theory of chemistry, in which substances came in quantal packets (molecules composed of integer multiples of carbon), and the discovery of point causation of infectious disease (bacteria) by Pasteur and Snow and others.  I think this general scientific environment led Mendel to think in terms of 'integral' causation, that is, by discrete causal units.

The work of Morgan and his students and colleagues was designed to explain how such point causes of inheritance worked, whatever they were at the molecular level.  In his fly experiments, also working with carefully selected traits as Mendel did (and aware that not all traits behaved this way), he used controlled, replicable experimental crosses to show that these sorts of point causes could be located to specific relative physical places in chromosomes.  This follow-up to what Mendel first clearly revealed was of course fundamental and extremely valuable.

Morgan did not, however, think of genes (the causal 'beads' on the chromosomal string, whatever their actual nature) as having a fixed functional effect. In the absence of direct knowledge of their chemical nature he, like Mendel and everyone else up to his time, had to use phenotypic markers to reveal the presence of a given allele (genetic variant).  He recognized that 'genes' could have multiple or complex effects, but he scored flies for traits that had some discrete, enumerable state at some specific life stage, such as newly hatched larva, in controlled crosses, that could be used to identify the presence of the causal element.  He didn't care, and was explicit about this, whether that was all the gene did, or whether the trait was even present at some other life-history stage.  One might say that he was interested in the causal layout or, shape, to use a word we used in a post last week, of inheritance.  That is, his approach was a tactic to understand the nature of genetic inheritance, essentially not to explain the traits.

Morgan explicitly also eschewed working in areas like developmental genetics--or stature--because he rightly said there was simply not enough known to do that at the time--more fundamental understanding was needed first.  By avoiding what was hopeless to understand at the time, and using his restricted, focused approach to get to a deeper question (genes as causal locations on chromosomes, recombination, etc.), he made some of the most important contributions to our understanding of life.

In that sense, it is fair to quote him as we did in our post because he both had the insight and the restraint to stay within what was known.

How did we get here?
The formal theories of genetics that developed in the early third of the 20th century included ways to reconcile discrete Mendelian heritable 'causation' with the causation of the more obviously continuous traits--like stature.  The reconciliation was the concept of 'polygenic' rather than point causation.  The idea, in its theoretical expression, was that an infinite number of infinitesimally small individual genes generated the continuous population distribution of complex traits.

Like points in geometry, genes could be point causes, but were infinitesimally small in the limit, and their joint effects could have useful distributional properties (like the bell-shaped distribution of stature).  But quantitative geneticists properly refrained from trying to identify individual genes 'for' such traits (or, as time progressed, claimed that sometimes one or a few 'major' genes might be identifiable but in a polygenic background).  Whatever they were, genes behaved in individuals and were transmitted in aggregate ways that clearly fit the polygenic model, whether or not the number of causes was literally infinite.  That's like saying a line can be understood and analyzed as if made of countless infinitely small, non-enumerable points. From an aggregate point of view, it makes complete sense.

By roughly the 1990s, while the human genome reference sequence did not yet exist, it nonetheless became technically possible to scan the whole genome for specific sites that contributed to complex traits.  The genome was viewed much more as a string of discrete beads than it is now.  Enthusiasm was high because the method worked (called 'linkage' analysis, in very large families where detection power is greatest) and breast cancer susceptibility genes, cystic fibrosis, and others as well, were mapped by various related approaches.

Without going into the historical details, what was mappable were genes in which there were sufficiently common variants with sufficiently strong effects to appear in families in a pattern much like that which Mendel had introduced, in which the trait was an efficient marker of the presence of the causal allele.  The predictive power was strong in those families, but it was just as obvious that this was not the general case for occurrences of the same traits.  Even today, the preponderance of breast cancer cases are not due to the BRCA genes nor does the disease segregate in families in Mendelian fashion.

Still, the mapping-drug had been taken, and geneticists on a high saw a limitless landscape of possible ways to identify--to enumerate--the genomic regions that contributed causally to a host of complex, largely continuously distributed (quantitative) traits.  Just collect more data!  As technology improved, the addiction was fed because endlessly finer resolution seemed in the offing.  The 'hits' that were made were naturally trumpeted with great enthusiasm.  We could turn complex traits into Mendel's peas!

This began in earnest around 15 years ago, and money poured into genetics: the omics era had dawned.  For legitimate as well as fashion and imitation, every problem was turned into a big-data 'omics' problem driven, rather than just enabled, by advancing technology.  Nutrigenomics, diseaseomics, microbiomics, epigenomics, proteomics, and so on.  In a sense, science has become industry, and has jumped on the 'Big Data' bandwagon.

Where are we now?
The problem as I see it is that we have reached what seems clearly to be a kind of ceiling in cost-benefit or signal to noise terms.  The findings over the past 20 years, both widespread and consistent, from natural as well as experimental approaches, and from all the kingdoms of life, have confirmed the century old theory that the traits in question really are 'polygenic' in the practical sense of the term.  This is an elegant success story--but it's more like Morgan than the transformation so vocally being asserted, which amounts to the promise of imminent medical miracles.

There will of course always be some important findings when such a huge enterprise is undertaken. But we seem not yet willing to acknowledge, much less accept the limits of the new knowledge, in particular including that predicting complex traits from genomes at birth is not going to go as promised.

People aren't saying, with restraint, that we're just showing that discrete spots on the genome have causal effects, because we have blurred the effect (e.g., stature, but only after problematic 'regression' on age, sex, etc. as if that were the equivalent to Morgan's marker traits), we have assumed that random sampling gives the same sort of information as controlled crosses and so on.  We have assumed that estimating these things retrospectively gives us estimable predictive ability.

At this stage, the view we've expressed is that we now have countless big-scale mapping studies, generating similar results, and it's time to think about what we've been shown, rather than to continue along the same basic path.  Some are doing that, advocating whole-genome sequencing and whole-population data bases of sequence--partly to avoid the problem with the association studies that they can't find rare causes, and hoping instead to find them in families within population data bases.  This, too, will work sometimes.  But this is asking for a lot for the occasional success. It is not asking whether what we've done has shown us that genomes work in ways far more complex than our enumerative approach is aiming to document--and that view is what we assert.

It is of course possible that the kind of data we are collecting is, in the end, appropriate and that there isn't anything profound yet to be discovered by more careful, focused, less industry-first methods. Time will tell.

A standard wagon-circling criticism of those who say we've done more than enough of the recent mapping approach, is to say that if you don't have the answer you should shut up and go home.  But that is somewhat like saying that if you sees that the theater is on fire, you shouldn't say anything about it unless you have a hose in their hand.  That's a totally bogus argument.  If there is a problem, and many do now think so, and nobody is seriously rebutting the points, then there is a problem! There are resources, fiscal and intellectual, at stake and that could be used more productively.  Denial and aggressive promotion of current practice certainly keeps the motor running, but it won't solve the problem.

Reductionism, part II -- The Tunnel of Love

Choosing to wear blinkers
Yesterday, we suggested that even the early geneticists were well aware of the multifactorial causation of traits, and asked how the 'gene for' thinking that has driven so much recent research, largely without satisfying results, came to predominate as it does currently. Today we suggest that science restricts its view intentionally, as a pragmatic way of discovering the nature of aspects of Nature. Indeed, the early geneticists did the same. And we point out that the price we pay is the way scientific methods restrict the degree to which we understand things more broadly.

'Gene-for' thinking is pragmatic -- understanding the molecular basis of genes and how they work is easier than understanding, say, polygenic interaction or the effect of the environment on development.  And of course great progress was made in molecular genetics throughout the 20th century, which only reinforced the view that the molecule was the thing. This, coupled with formal population genetics, gave researchers rules (how genes segregate, how DNA codes for proteins, and so forth) for cataloging how genes work, giving the field a theoretical framework within which to plan, execute and interpret experiments.

Discoveries in other fields sometimes reinforced the determinist view as well. Following not long after the 'one gene one enzyme' dictum was hypothesized by Beadle and Tatum in 1941, e.g., the coming of the computer age underscored the view of genes as the program or blueprint for life, an appealing and seductive idea that is yet to die. Even if a blueprint needs an architect, and a foreman to supervise the building.

In fact, the idea that the early geneticists had a broader view is only partially true. That they did is well-documented, as we wrote yesterday, but it wasn't ever really put into practice. Then as now, experiments were conducted in a way that enabled these guys to find single genes that 'caused' the traits they were interested in; environment was controlled, and fruit fly lines homozygous for a trait known to be due to the effects of a single gene were crossed so that the effect of a given gene could be assessed, just as Mendel had done with his pea plants.

This is how Morgan mapped genes. And, why those genes were given names like 'hairy wing', 'small eye', 'small-wing', 'vermilion', as though they were the single cause of or were 'for' these traits, even though Morgan knew full well that wing characteristics or eye color were due to many genes. Indeed, he wrote in The Theory of the Gene, "... it may appear the one gene alone has produced this effect. In a strictly causal sense this is true, but the effect is produced only in conjunction with all the other genes."

The question thus becomes a philosophical one about causation. Philosopher of science Ken Waters has written a nice paper about this*, discussing the difference between 'potential' and 'actual difference makers' and how experimental method determines which is found, while prior assumptions determine which are sought. Although Morgan knew that it took many genes to change eye color in flies -- potential difference makers, in Waters' terminology -- the gene that actually changed eye color in his experiments, a direct consequence of the way he conducted them, was the 'vermilion' gene. The actual difference maker. The foundation for gene-for thinking was well-established right from the beginning, and reinforced all along the way.

And, of course, the idea that some of the early eugenicists may have understood that environmental influences could be important in development didn't prevent the Nazis from making life and death decisions based on heredity.

'Gene-for' fervor takes off -- and people actually believe it
After the discovery of the gene for cystic fibrosis in the late 1980s, genes for more than 6000 single-gene disorders were quickly identified. These are largely rare, pediatric diseases, but even so there seemed to be little reason to assume that geneticists wouldn't continue finding genes for disease, and then even for behavior and other kinds of 'normal' traits, even if an important aspect of pediatric disorders is that they occur near birth and hence are relatively less susceptible to environmental effects (not entirely, of course, because even the uterine environment can vary).

This kind of success at finding genes associated with traits was seductive, and the commitment to strong genetic determinism is now found not only among geneticists, but among epidemiologists, psychologists, economists, political scientists, and even further afield. Epidemiology, e.g., had its own history of success finding the cause of infectious diseases, as well as the effects of environment risk factors like asbestos or smoking. But, as with single-gene disorders, when the effect of a risk factor is large, it's a lot easier to find than when there are many cumulative risk factors, some genetic and some environmental. When epidemiology turned to common chronic conditions like heart disease, asthma or diabetes, which generally don't have a single strong cause, they ran into the same kinds of epistemological and methodological difficulties that geneticists were having with these same complex diseases.

Ironically, out of frustration with the difficulty of finding environmental causes for many chronic diseases, epidemiology turned to genetics, and the field of genetic epidemiology quickly grew. Only to be as stymied in terms of the fraction of cases explainable by known genes. The 'strictly numerical basis' upon which Morgan had identified so many putative genes was no longer good enough. Because the counts don't come out in Mendelian terms unless fudge factors (called 'incomplete penetrance', a determinist idea itself, as it imbues the gene with a mystical ability to be more or less expressed) are added to account for other causes relative to a gene under study, usually meaning the gene accounts for only a small fraction of cases and doesn't have nearly Mendelian ratios among siblings, etc.

And it becomes institutionalized
Then of course when the Human Genome Project was finished, the sequencing factories had to be kept running, so yet more promises were made about what we were going to be able to do with genes, more billions were spent on more classically reductionist 'count only' genetics -- and yet the same problems remain unsolved. We still can't enumerate the genes that are responsible for height, and for exactly the reasons Morgan spelled out in 1926, as we noted yesterday.

In fact, the scientific methods that we use identify genes that, when mutated in some ways, cause serious stature problems (Marfan's syndrome makes you very tall, many genes make you very short), but when we look at the normal range as seen in a sample of healthy people, these genes do not generate mapping 'hits' (as in GWAS association studies). And this is probably true of most traits -- it's easier to explain the extremes of their distribution than it is to explain the normal range.

It's not that genes are unimportant. It's that we are only taking into account part of the truth. This is driven essentially by methodological considerations -- we've got well-developed formal theory for genes and how they segregate in families, and what that means about how to find them. But it is more of a struggle to account in useful ways for complex causation -- useful, at least, in terms of dreams of miracle drugs or genetically focused personalized predictions.

Tunneling through the truth

An important reason for the combination of great success in discovery in genetics, and the relatively great failure to account for complex traits has to do with methodology rather than the state of Nature. As we said yesterday, the focus on fixed, chromosomally localized causal elements -- 'genes' in the classical sense -- was driven by Mendel's careful choice of experimental material, followed by similar constraints employed by Morgan and the other classical geneticists of the early 20th century.

The very same logic and approaches have been followed to this day. Genes are identified as localized causal elements in DNA and we study and manipulate them through variation that is studied, as much as possible, by removing all other sources of variation. Traits are narrowly defined, transgenic experiments use inbred animals manipulated one gene (or one nucleotide) at a time, and so on. This is done because it generates a cause-effect situation that is tractable.

That approach, or research program, led to the steady discovery of the nature of DNA, of genes as protein codes, and so on, up to the mapping of entire genomes of a rapidly growing number of species.

Yet at the same time, when it comes to complex traits, we know that we are not discovering the whole truth -- and we know why. It is the same control of variation that led to discovery, that leads to obscuring the whole nature of Nature.

In a sense, what science does is to 'tunnel' through reality. Like any other tunnel, the walls are reinforced to keep things outside the tunnel out, and to make a clear path within. The path is a particular gene we are interested in, and we manipulate that gene, and its variation, treating it as a cause, to see what effects it has. We know it really interacts with the world outside, but we standardize that world as much as we can, to reveal only the effect of variation in the single cause.

This is perhaps a tunnel of love of experimental design, but not so much of the nature of Nature, because by particularizing findings, even on a large scale, we systematically isolate components from each other whose true essence, and origins, are intimately dependent on their interactions.

Maybe tunneling through truth is the only way science can understand the world. From the point of view of garnering facts, and manipulating the world by manipulating the same facts, science is a huge success. But in terms of understanding Nature, maybe we need a different way. If so, as long as the reductionist legacy of the 300 year old Enlightenment period in human history lasts, we will remain the Tunneling species.

Tomorrow we'll discuss how the same kind of thinking has worked in developmental genetics and the EvoDevo world of research.

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*The Journal of Philosophy is only available online to members, but the reference is Waters, "Causes That Make a Difference", The Journal of Philosophy, 104:551-579, (2007).

Genetic reductionism, part I -- the path from broad to narrow?

What geneticists used to know
We've been reading the writings of some of the early geneticists, and have been struck by how many of the original concepts and how much of the jargon are still in use even after a century of major discoveries. Even many of the names TH Morgan gave to fruit fly genes in the 1910s and 20s, without knowing anything about the structure of genes and how they work, are still in use today. Their names, in fact, are a major reflection of the way that science actually works.

The figure to the left, a map of the four fruit fly chromosomes, with gene names, is from Morgan's book, The Theory of the Gene, published in 1926. In that book, he outlined his theory as follows:

The theory states that the characters of the individual are referable to paired elements (genes) in the germinal material that are held together in a definite number of linkage groups; it states that the members of each pair of genes separate when the germ-cells mature in accordance with Mendel's first law, and in consequence each germ-cell comes to contain one set only; it states that the members belonging to different linkage groups assort independently in accordance with Mendel's second law; it states that an orderly interchange--crossing-over--also takes place, at times, between the elements in corresponding linkage groups; and it states that the frequency of crossing-over furnishes evidence of the linear order of the elements in each linkage group and of the relative position of the elements with respect to each other.

Note that his theory of the gene rests almost entirely on the work of Mendel, fifty years before. By good luck (given what was known at the time), Mendel studied traits that were not closely located ('linked') on the same chromosome, so that Morgan's group was working with and expanding on rather then testing or challenging Mendel's theory.

Mendel knew that systematic hybridization experiments would elucidate patterns of transmission of the 'elements' that were responsible for traits. But only some traits; others were too complicated, and didn't follow the same patterns. Mendel tried the same approach in other plants and found that some did not follow his rules, in fact; but the doubts that led to were overlooked given his overall success. We now know that traits he avoided did not 'segregate' in the way the traits he chose did, because they are due to the joint contribution of many different genes, known today as polygenes.

Morgan presents his theory of the gene, and then adds the following, and this is important with respect to how they could know as much as they did without understanding much at all about genes:

These principles, which, taken together, I have ventured to call the theory of the gene, enable us to handle problems of genetics on a strictly numerical basis, and allow us to predict, with a great deal of precision, what will occur in any given situation.

By 'strictly numerical', he meant that one need not understand what the genes were, in chemical terms, or how they worked. The rules of inheritance were made manifest through the relative numbers of different types of offspring of a given set of parents -- which Mendel first showed, and others built upon.

But Morgan didn't suppose that all traits were due to single genes. He was aware that most were due to many genes, and that it was likely that most genes do more than one thing.

A man may be tall because he has long legs, or because he has a long body, or both. Some of the genes may affect all parts, but other genes may affect one region more than another. The result is that the genetic situation is complex and, as yet, not unraveled. (The Theory of the Gene, p 294).

And, these early geneticists also knew about the fundamental contribution of the environment. Morgan ends the paragraph above with this sentence: "Added to this is the probability that the environment may also to some extent affect the end-product."

A student of Morgan's, A.H. Sturtevant, in his A History of Genetics (1965), says:

With Johannsen [who introduced the words "gene", "genotype" and "phenotype" in the early 1900's] it became evident that inherited variations could be slight and environmentally produced ones could be large, and that only experiments could distinguish them.

And:

In 1902 Bateson pointed out that it should be expected that many genes would influence such a character as stature, since it is so obviously dependent on many diverse and separately varying elements. This point of view was implied by Morgan in 1903 (Evolution and Adaptation, p. 277), and by Pearson in 1904.

This is among other early examples he offers. Even the most widely used genetics textbook in the 20s and 30s, a book in fact that helped school the Nazis (and a chilling read today), described variation in traits that were due to environmental factors. That book was Human Heredity, by Baur, Fischer and Lenz, first published in Germany in 1921, and revised a number of times. Two of their examples of traits with environmental contributions, are pictured to the left. The pigs in the top photo to the left are from the same litter. The smaller one was poorly nourished, while the larger one was well-fed. As for the rabbits:

Among rabbits, for instance, there are two somewhat similar races, one of which is pure white with pink eyes, while the other (the "Himalayan" rabbit) though mainly white and whit pink eyes, has very dark fur on the ears, paws, tail, and nose. The colour of the fur in this latter race is modifiable by temperature. If an area of its skin be kept cool, which can easily be effected simply by shaving a part, all the new hairs that grown upon the cooled area have a dark tint. Fig. 6 shows how a patch which had been thus shaved has been covered with dark hair. But as soon as the fur has regrown, so that the area of skin is now protected by it from the cold, all the new hairs which subsequently grow in the area are white, as before, so that the dark tint of the shaved area gradually disappears. It would be easy enough, by shaving the whole surface of the body, to provide one of thees rabbits temporarily with a dark-tinted fur throughout... P 33-34.

So, how did this broad view of genetics become so much narrower as the field matured, so that genetic reductionism that now predominates to a great extent? Indeed, the Human Genome Project and its ongoing sequels epitomize this approach, as its supporters promised that knowing our genes would lead directly to disease prediction (and prevention, and even dramatically increased longevity as a result). Whether this was truly believed, or was cynical spin to get funding -- in fact, it was a mixture of both -- even the intellectual forebears of today's geneticists knew it was wrong.  Or was the early view never as broad as it seems?

In our next couple of posts we'll have some ideas on this. You may disagree, or have other ideas, and if so, we'd love to hear them.

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This post was stimulated by work on a paper about the developmental genetics of complex traits like the mammalian skull, and by interactions Ken had on his recent trip to the University of Minnesota, with two philosophers of science Ken Waters and Alan Love.