Tuesday, January 31, 2012

Did Darwin run a pyramid scheme? Darwinian method, continued

Before the period of the Enlightenment in science, roughly starting with Francis Bacon and Galileo and others, about 400 years ago, a model of knowledge (among scientific types, at least, not farmers and craftsmen and others who actually earn a living) was largely attributed to Aristotle from around 400 BC.  According to this view of how we should figure out the world, we were hard-wired to understand the nature of Nature (sounds like a lot of genetic or Darwinian determinists, doesn't it?).  Thus, knowledge could be deductive (the classic example of this is 1) All men are mortal, 2) Socrates is a man, 3) Therefore, Socrates is mortal).  The basic truths were known and were in that sense axioms from which predictions about facts to be found could be deduced.  In a sense, the facts were latent in the assumptions.  A theory came first, and led to many facts.  (The BBC Radio 4 program, In Our Time, featured a nice discussion of the Scientific Method last week.)

But the Enlightenment turned that idea on its head.  The idea was the scientific method that started with observation rather than inspiration, and built up a pyramid of understanding.  First, by the process of induction, many observations were made, seen to be consistent, and they lay at the base of knowledge (All the swans I've ever seen are white, therefore all swans are white).  Other types of generalization built upon this base, to the top of a pyramid of understanding, the final theory that we infer from facts.

When Darwin published his theory of evolution, of descent with modification screened by natural selection, from a common ancestral form, it was a challenge to accepted wisdom.  The scientific method was well established, but religious explanations of life were rife.  Darwin's theory certainly challenged this big-time!

Now, Darwin amassed countless facts--it was one of his incredible fortes.  From these he inferred his theory, and on the face of it this would seem to be the scientific method if anything was.  But the geologist and former friend and teacher of Darwin's, Adam Sedgwick, was rather incensed by the theory of evolution.  Sedgwick was a seriously Christian believer, and could not abide this threat to all that he held dear.  He lambasted Darwin, not explicitly because Darwin contradicted biblical explanations, but because Darwin's theory was (in our words) Aristotelian rather than Baconian:  it was incorrect, old-fashioned and not real science at all!

Inverted pyramid, the Louvre
Sedgwick basically argued that Darwin inverted the proper pyramid of knowledge.  He claimed to be using inductive reasoning by bringing to bear so many different facts to form a consistent theory.  But in fact, argued Sedgwick, this was not induction at all!  That's because Darwin used the outcome of life that he observed as if he could draw conclusions from it inductively, when in fact life had only progressed on the Earth once!  Thus, Darwin was taking a single observation, partitioned into many minute facts to be sure, but was generalizing about life as if evolution were observed again and again.  This, said Sedgwick, was old fashioned a priori theory driven reasoning that Aristotle would be proud of, but it did not have the empirical truth-value that the scientific method was developed to provide.

In various discussions of this topic then and since, it appears that Darwin largely conceded the formal point, but of course stuck to his guns.  He could (and we can) predict new facts, but they are details that can immediately be fitted (or, Sedgwick would perhaps argue, be retro-fitted) into the theory.  Yes, there was diversity in the world, but this could arise by other processes (such as special Creation) and the theory of evolution was not the only explanation as a result.  It was not, argued Sedgwick, properly inductive.

One could argue that we have used this theory in so many ways, modeled mathematically and experimentally in artificial selection, to predict formerly unknown phenomena about life, that the theory has clearly stood the test of time.  Many facts about the one process on earth, could be used to generalize about the process as if it could be repeated.  We argue that different species in different places each do represent replicate observations from which the process of evolution can be induced.  Or, one could argue, inductive reasoning is just one way of getting at convincing accounts of the nature of Nature.

One might even go all the way with Aristotle, and say that for the very reason that evolution did occur, our brains were adapted (by Darwinian processes!) so that we are built to understand Nature!  The argument probably wouldn't hold much water, but it's a thought.  In any case, the fact that evolution only occurred once does suggest that the idea was cooked up by Darwin in a non-inductive way--even if his theory was built upon countless observations, but of one single process.

The triumph of the Darwinian method, to use the title of a book by Michael Ghiselin that we posted on in October and November 2011, proliferates throughout the life sciences.  There are things that this allows us to do that are not exactly inductive, but are close to inductive reasoning in many ways.  This has to do with the nature of variation and how it's to be explained.  In a next post we'll discuss this in light of DNA, totally unknown to Darwin.  There are substantial problems, and many of the inferences we make about specifics of the past are speculative, but overall, Darwin was not a Madoff, and did not hustle us with a pyramid scheme! 

We'll see how Darwinian concepts, more than any other, enable us to understand why DNA sequence can be 'random' on its own, in the sense that the A,C,G,T's along DNA are by various statistical tests  random: the nucleotides in one place don't predict those nearby or elsewhere along the sequence.  Yet the nucleotides are not just letters in a computer test, and are in fact anything but random.  Indeed, the concept of randomness has to be revised because DNA sequences evolved.

Monday, January 30, 2012

Playing on the real strings, or just your heart strings?

A recent study of whether a combination of professional and amateur violinists preferred old or new violins has gotten a lot of press, here first in the NYT, and then again yesterday.  The study was double-blinded, and 'scientifically run', and claims to be the first to properly test the hype about Stradivariuses.  Touted as 'gotcha' results, showing that people only think Strads are great because they are expensive, the study, published in the Proceedings of the National Academy of Sciences, reported that experts can't tell whether they are playing a priceless Stradivarius or a violin by a modern maker.
We found that (i) the most-preferred violin was new; (ii) the least-preferred was by Stradivari; (iii) there was scant correlation between an instrument's age and monetary value and its perceived quality; and (iv) most players seemed unable to tell whether their most-preferred instrument was new or old. These results present a striking challenge to conventional wisdom.
Here's the NPR treatment, complete with a sound test.

So, the most recent NYT story apparently accepts the comparative study, but it turns out that, according to our daughter Amie who is a professional violinist, by and large the world of professional musician does not.  In fact, one of the participants in the study says here that they were not asked to identify the old violins, they were asked to choose their preference.   She describes her experience:
Upon arriving, I was fitted with modified welders' goggles, and I entered a darkened room. I was then presented with 10 pairs of violins. For each pair, I had a minute to play whatever I wanted on the first violin, then a minute to play whatever I wanted on the second, without switching back and forth. After playing each for one minute, I was asked to choose which of the two I preferred. Then on to the next pair -- 10 times altogether. I thought I was testing 20 violins!
As it turns out, I was testing 6 violins, just paired up differently each time. One always was an old violin, the other was a modern, and they used different combinations against each other.
She points out that the old instruments weren't optimized (sound post adjusted, new strings, etc), while the new instruments were.  
The test was not over after the 20 violins, which were really six violins. After that part of it, the six violins were laid out on the bed, and I was given 20 minutes to play with them as I liked. My task was to choose which of these violins I would take home if I could, and also to decide which of the six was "best" and "worst" in each of four categories: range of tone colors, projection, playability and response.
She preferred one of the moderns, although she did say in her comments for the investigators that she thought it had potential, not that it was already great (good violins improve with time as they are played, although modern violins can either improve, or they can lose their sound, so the reputation of a modern maker is only enhanced if their violins stand the test of time).  That is, this violinist suspected it was a modern violin.  And, she points out that they were not asked whether they could tell the difference, just which they preferred -- despite the inferences all over the web that even professional violinists can't tell old from new, and only like Strads because they are expensive and have a mythic reputation.

Another one of the participants, "an accomplished amateur violinist and violin maker", believes the study was well-run and the results perfectly credible, as he says here.

So, what's going on?  Was this a valid study or wasn't it?  Does it bust the Stradivarius myth?  Some violinists have pointed out that testing instruments in a small hotel room, where their sound can't project, seriously hinders a player's ability to judge.  Others that the researchers'  conclusions weren't properly inferrable from what the players were asked to judge, and of course if that is so, no matter how 'scientifically valid' the study was, the conclusions are largely the researchers' interpretations rather than objective findings.   And, some of the participants were amateurs, and even if they were excellent musicians, their experience with playing in concert halls, where an instrument really makes a difference, is necessarily limited. Of course, musical quality is largely subjective and perhaps knowing the instrument is a Strad can make some people enjoy it more.  And, the impartiality of the researchers, some of them modern instrument makers, might be an issue.

The quality of the sound of a string instrument depends on many variables, not least of which is the listener's preferences.  But also, the bow with which it's played, the adjustment of the sound post, the quality of the strings, and even what kind of strings, what the player chooses to play, and whether it's the same piece on each instrument.  And so forth.  And of course, Strads have been fixed, tuned, adjusted, revarnished, and so on so that today's Strad is not the same as what Stradivarious himself built.

This is not like judging red wine, which can just be poured into a glass, allowed to breathe for a set number of minutes, and then tasted.  Preference for wine is still subjective, but at least the factors that can influence its taste are part of the essence of the wine, unlike the music that comes out of a violin. If fact, it's been shown repeatedly that blindfolded, even experts can't reliably tell if a wine is great or just good, or often, even if it's red or white!

Scientific methods can be applied to a multitude of questions, but the question has to be clear, the variables controlled, and the subjectivity of the answers at a minimum.

PNAS hitting the bell of deep science yet again!  Still, if not the most profound kind of science, mythbusting is important, even if it's not in the interest of vintners or, in the case of violins, of auction houses.  But, should this study be considered the final word?

Friday, January 27, 2012

Hot flash (not hot flashes) of the week: Who stops at red lights?

Well, dear MT readers, we hate to shock your tender sensitivities, but some times we feel absolutely forced to confront you with truths that you may wish were kept hidden.  So here goes:

A new paper by Shutt et al., in Biodemography and Social Biology, reports from a whopping sample of  612 men and 601 women, adolescents or very young adults, who self-reported about their sex-purchasing activity (was this marketing research?), that males pay for hookers much more than females do. We were blown away by this finding, but then even more impressed by the fact that this contemporary US survey of whopping size proved evolutionary theories about sex and parental investment.  Men  can just say screw the consequences (so to speak), while women are left changing the nappies (while the guys are out screwing other consequences).

But then why are the women in the trade, given these evolutionary 'drives'?  Are they all forced, and if so how does that relate to evolution, since part of evolutionary theory is that males want their women to be chaste so they know who's the father of their children?  Or is this a financially viable career option for those who can't get a comparable job in banking (a similarly moral profession)?  Madams themselves are female, and they're doing the organizing. 

Our point is not to question the results of this paper, given their sample and the question they asked.  Rather, it's to question their relating this to more general theory.  Whether or not the behavioral evolutionary theory itself has merit, this seems like a misrepresentation of what we can, and can't, actually say about how evolution really worked as contrasted with how we think it might (should, or even 'must') work, and what kind of data we'd really need to say it. These kinds of data are possibly consistent with that theory, but hardly constitute strong support (or not) of it.  But publication of such speculations, which is routine these days, can give an impression to readers who don't know enough to be skeptical, that we know more than we really do.  The burden for such misrepresentations rests on the scientists and the journals that publish the work.  And when it comes to evolution-based determinism regarding behavior, history clearly proves that can have dangerous societal implications, in which the powers that be decide who's OK and who's not, and what to do (to them) about it.  Are hookers hookers because of their genes?  Are the guys customers because of their genes (that is, the genes that 'make them do it', not those they shed in their business transactions)?  If their genes made 'em do it, is it something 'we' have a right to 'treat'?

Science representing itself as representing something generic and fundamental, should at least have data that are appropriately representative of that principle.  There are many reasons that males and females may have different reasons for stopping, or not stopping, at red lights.

Thursday, January 26, 2012

That's disgusting! Make up your own Just-So story about the evolution of an emotion

The evolution of disgust
Everyone seems to be talking about disgust these days, from why it evolved to what parts of our brains light up when we feel it (it's the anterior insular cortex).  There was a story in the NYT about it on Tuesday ("Survival's Ick Factor"), and a review of a new book (one of many) about it in the Sunday NYT Book Review, a conference in Germany, and an issue of the Philosophical Transactions of the Royal Society devoted to the subjectDarwin included disgust in his list of the 6 basic human emotions, and wrote of seeing it on the faces of his infant children. 

Indeed, it seems that disgust now explains many human characteristics from tribalism, to disease avoidance, to poison critter avoidance, and mate choice.  And, disgust gone haywire explains psychological pathologies from obsessive compulsive disorder to excessive anxiety.

A paper in Perspectives in Biology and Medicine in 2001 lists the basic disgust elicitors. 
We suggest that the objects or events which elicit disgust can be placed in the following five broad categories:
1. Bodily excretions and body parts
2. Decay and spoiled food
3. Particular living creatures
4. Certain categories of "other people"
5. Violations of morality or social norms
Bodily secretions are the most widely reported elicitors of the disgust emotion. Feces appear on all of the lists, while vomit, sweat, spittle, blood, pus, and sexual fluids appear frequently. Body parts, such as nail clippings, cut hair, intestines, and wounds, evoke disgust, as do dead bodies. Certain animals are repeatedly mentioned, in particular pigs, dogs, cats, fish, rats, snakes and worms, lice, cockroaches, maggots, and flies. Spoiled food, especially meat and fish, and other decaying substances, such as rubbish, are disgusting to many respondents. Certain categories of other people are also found disgusting, notably those who are perceived as being either in poor health, of lower social status, contaminated by contact with a disgusting substance, or immoral in their behavior.
And then there are sensory cues, smells, feel, sounds.  A number of writers explain that all these things are disgusting because they remind us of our animal -- unhealthy? -- origins.  Others say it evolved to defend body and soul from pollution (as apparently being reminded of our animal origins pollutes the soul).  
In their exploration of Darwinian medicine, Nesse and Williams (Evolution and Healing, 1995) suggest that an instinctive disgust may motivate the avoidance of feces, vomit, and people who may be contagious, and that disgust is one of the mechanisms crafted by natural selection to help us keep our distance from contagion. Pinker (How the mind works,1998) proposes that disgust is "intuitive microbiology," and that this explains our aversion to objects that have been in contact with disgusting substances: "Since germs are transmissible by contact, it is no surprise that something that touches a yucky substance is itself forever yucky." 
It's nice that this emotion is finally getting the attention that it clearly deserves.

But wait a second!
Except -- there had to be an except! -- except that a lot of this starts to sound suspiciously like just another elaborate evolutionary Just-So story.  New parents, nurses, physicians all quickly lose any disgust at bodily excretions, and one person's spoiled food is another's delicacy.  Just think of the rich array of foods that people on this planet eat.  Not to mention dogs, who'll eat just about anything.  Dogs share many of our emotions, and, if essentially all humans feel disgust, our sense of disgust had to have evolved earlier than we did, so shouldn't other lineages who share our disgust-feeling common ancestor, such as dogs, also share our supposedly instinctual disgust with eating, say, rotten meat, or vomit?

Dead Zambian shrew, not Holly's shrew
Which may explain why Holly reports holding up a dead shrew to her two dogs and finding that they wouldn't touch it.  She says her dogs would happily tear apart a dead squirrel, but not the shrew.  She thinks maybe it died of pesticide poisoning, though she couldn't smell anything.  Were they disgusted (by at least this one thing!), thus saving themselves from pesticide poisoning?  Or is it that they have learned to tear apart squirrels and not shrews?  Who knows?

But then, why is it disgusting to some people to eat insects, while others thrive on them (roasted, chocolate covered, etc.)?  Or why did Americans once disdain disgusting lobster....and now drop big bucks for a nice, juicy claw?  European Americans recoil at the thought of eating horse meat, while to many of their Old World brethren it's a delicacy. Or what about latakia pipe tobacco and lapsong suchong tea, 'cured' as one might say, over dung fires?  The list could go on and on and on, but what it means is that there's an obvious learned component.

But, let's agree for the sake of argument that disgust as an emotional reaction in fact evolved as a specific trait.  And even that disgust might have its uses (though, too much of it can be a problem).  All this means is that, as other successful traits that have stood the test of evolutionary time, disgust itself is adaptable.  That is, yes, we may all feel disgust, but what disgusts us at any given time is culturally determined, not innate.  Otherwise, how could we learn that Twinkies were disgusting?  (Or not.  It turns out that if you search in Google Images for Twinkies, you'll find a photo of Twinkies Fondue; Twinkies, circus peanuts, caramel Ho-Hos, marshmallows, and candied orange slices on a skewer, waiting to be dipped into molten chocolate.  Or Scottish deep-fried Mars bars!  Who thinks these things up?)

Our better idea!
And any of us can think of alternative hypotheses as to what disgust is 'for'.  Here's ours -- how about that it's part of our repertoire of communication, rather than an innate ability to save ourselves from decaying meat?  Why would we need a facial expression that communicates disgust if the emotion itself were the survival tactic, alerting us not to eat that rotting wildebeest?  Surely we could teach our children that even bunny rabbits were disgusting, if we started them young enough.  So, in adaptive terms, it's communicating that we're disgusted that's important, not what we're disgusted by.  Why?  Because it elicits caretaking, a survival tactic if there ever was one. And of course survival is very directly tied to evolutionary fitness.

But all this hoopla about disgust is a bit disgusting itself.  Are we really desperate to have specialties so that someone can be called by the NY Times "a pioneer of modern disgust research"? It's one thing to specialize, even to this extent, and perfectly legitimate to identify 'disgust' and try to understand its neurophysiology and physiological triggers -- if there really is an 'it'.  But it's quite another big step to attempt to Darwinize something so vague, and the fact that Darwin mentioned it doesn't change that.  Evolutionary scenarios are hard to pin down, even with well-defined traits.  The evidence by and large suggests that most of the human versions of this emotion, if it is a particular emotion, are learned and experiential and culture-specific -- adaptable. 

Obviously the inherent aspects, the 'adaptive' aspects of our disgusting behavior are unclear, hard to identify, harder to prove, and in any case it is not obvious that we have any such adaptations that were not in place eons before a human ever stepped on a wildebeest patty (barefoot--UGH!).

Wednesday, January 25, 2012

Spontaneous combustion! Life is not the same as organized life. Part II.

The idea of spontaneous generation as debated by philosophers before the age of science referred not just to life as a particular kind of self-sustaining chemical reaction, but to that process as manifest in highly organized--differentiated--organisms:  trees, beetles, worms, and all of us.

Maggots--disgusting as they may be--are highly organized forms of life with anatomic structures, highly specialized cells, and that develop by developmental differentiation through sequential patterns of gene expression.  The idea of spontaneous generation referred to such complex creatures, and by extension to all organisms, not just bubbling primal soup.

Even if such soup were to exist today in little cauldrons in the rocks or sea, it would not produce such organisms.  That is the key difference between life as a chemical phenomenon--which it most clearly is--and life as a complex ecology of different organisms, each of which is itself an internal ecology of different organs, which are ecologies of different cell types, and cells have their own internal ecology of subregions, specialized functions, and the like.  This is true even of bacteria, singly and in aggregates, fossils of which have been found from as early as 3.8 billion years ago.  Those don't arise spontaneously!  And that is the very central key to why life is not like crystal formation, volcanoes, and solar systems.  And, of course, it's the deeply insightful awareness of this, by Charles Darwin and at the same time by Alfred Wallace, that we call 'evolution', that was one of the most transforming insights a human being ever had.

Life is about continuation of a reaction--that's, after all, what you are relative to your parents, and their parents, and theirs, and......so on back to the initial lively cauldron.  And more importantly, centrally, life is about the accumulation of divergence of subsets of this reaction.  Divergence requires isolation (we called it partial sequestration in Mermaid's Tale), and transmission with memory (largely resident in DNA) that preserves divergence.  And the way that such divergence with memory accumulates in the kind of life we have here on earth, at least, is brought about by the fact that the basic processes of life are combinatorial and polymeric (see our prior series on this topic).

Genes and the proteins they code for are polymers, long molecules of sequences of a few possible subunits, whose behavior depends on, resides in, and is all about the number, location, and arrangement of particular substrings along the polymer.  That is what accumulates 'information' over time and produces functional subdivision like tissues and organs.

No matter what you may think of maggots (some people actually eat them!), they are marvelously organized, complex forms of life.  New flies are not spontaneously generated; instead, they are just cellular continuations of parent flies.

Any spontaneous generation of new 'living' (biochemical) reactions would simply be simple.  Organization of sequestered substructures and the DNA and protein polymers that make that possible, took hundreds of millions of years, if we can trust the earliest fossil evidence, found by our friend Bill Schopf at UCLA and others.  What we don't allow in modern biological thinking is spontaneous generation of highly organized life.  It must be possible in principle: after all, you and we are just chemical reactions that were generated by the chemical reactions in the eggs that founded us and all the way back to the first soup.  But the probability that a bunch of molecules randomly bouncing around in some puddle in your back yard would generate a bacterial cell, much less a bunny rabbit, is astronomically small (if the universe is truly infinite, however, that must be occurring infinitely many times at this very instant and at every instant--think about that for a while!).

In boring mundane terms, at least, it's not happening here.  Nor are organized structures like, say, bunny ears, being generated out of a tadpole pond.  No, these things are products of very long histories, not short-term instances. 

We need to carry the point forward, because it has fundamental lesson for our view of how evolution works and, generally, is strong support for and reflection of a key point in Darwin's founding theory of evolution.  It's that complex structures arise gradually.  If bunny ears or even just maggots could arise spontaneously, Darwin rightly thought, religious Creationist arguments would be more plausible than historical evolutionary ones.  But the facts show that the evolutionary arguments are the only plausible ones of those that have been offered so far.

Even when complex traits do seem to arise out of nowhere, such as extra vertebrae in the backs of children that were  not present in their parents, this is not spontaneous generation in the usual sense, because these are just anomalous repetitions of processes--like the one that generates vertebrae--that stutter more than usual.

This is why we never find, say, an organ from some dead organism that is totally unlike anything ever seen before.  Nowhere on the tree of the major life-forms that we know of (image grabbed from the Smithsonian Museum's webpage: http://www.mnh.si.edu/exhibits/darwin/treeoflife.html).  Or, less fantastical, we would never unearth a long DNA sequence that was totally unrelated to that of any known type of organism--that could not be shown to fit somewhere in the 'tree' of DNA sequences from plants, animals, and microbes for which we do have sequence.  DNA sequences carry the information for organisms, coding for their traits, and must reflect their history.  

If  we really found a long DNA sequence with no similarity to those we know of, and no structure (such as protein coding elements) that are universal to the life we do know of, we would be in a real quandry: it would be some trick, some product of a  DNA sequencing machine rather than a remnant of actual life, or we would have to rethink our entire theory of the history of life.  It would be very exciting and upsetting--a lot of fun to live through--but there's no sign of it happening.

So this is the deeper sense in which biologists can seriously say that, yes, spontaneous generation did occur once, but no, it is not an explanation for subsequent life.  We're not having our cake and eating it too:  we're saying that a cake takes time to bake!

Tuesday, January 24, 2012

Spontaneous combustion! How life began, how life begins.... Part I.

How did life begin?  People who don't find the answer in the Bible often believe they'll find it in Darwin's Origin of Species, but of course Darwin doesn't touch on the origin of life at all.  In fact, he doesn't even explain the origin of species.  But that's a story for another day.

For centuries it was viable to speculate that life arose by spontaneous generation. Stuff in the soil, for example, came together to produce organisms.  Of course, the knowledge at that time did not permit definitive study of the question.  But one example was the apparent spontaneous appearance of maggots in dead meat. Ugh!

However,  in 1784 Lazzaro Spallanzani performed a famous experiment (duplicated below by Ken a few years ago, as he described here) that showed these maggots only arose if the meat was exposed to flies, who laid their tiny, unobserved eggs on it.

The maggots did seem to appear spontaneously, but Spallanzani showed that if gauze were placed over the meat, no maggots (Whew!).  Thus, we needed another explanation, and in the age of science another type of spontaneous generation, Creation of species as individual acts of God, wasn't acceptable either.  Now, anyone who argues for spontaneous generation is gently ushered to the psychological services center.  But the story isn't quite so clear cut!

In our book, The Mermaid's Tale, we point out that people no longer believe in spontaneous generation .... except at the beginning, when organic life sprang spontaneously from inorganic elements.  Of course we were not the first to notice this inconsistency.  In fact, Thomas Mann wrote of it much more eloquently 85 years before we did.

In his beautiful book, The Magic Mountain, Mann tells the story of Hans Castorp, a young naval engineer just embarking on his career.  He pays a visit to his cousin in a TB sanatorium, intending to stay for 3 weeks and then return to work, but he ultimately spends 7 years there.  Being set as it is in a place of illness, where both healing and death are integral parts of life, the book is full of musings about the meaning of life, death, time, work, illness, science, art and much more.

Here's Mann on the origins of life (from the John E Woods translation).
What was life?  No one knew.  No one could pinpoint when it had emerged from nature and struck fire.  Nothing in the realm of life was self-actuated or even poorly actuated from that point on.  And yet life seemed to have actuated itself.  If anything could be said about it, then, it was this: life's structure had to be so highly developed that nothing like it could occur in the inanimate world.  The distance between an amoeba--a pseudopod--and a vertebrate was minor, insignificant in comparison to that between the simplest form of life and inorganic nature, which did not even deserve to be called dead--because death was merely the logical negation of life.  Between life and inanimate nature, however, was a yawning abyss, which research sought in vain to bridge.  people endeavored to close that abyss with theories--it swallowed them whole, and was still not an inch less broad or deep.  In the search for some link, scientists had stooped to the absurdity of hypothesizing living material with no structure, unorganized organisms, which if placed in a solution of protein would grow like crystals in a nutrient solution--whereas, in fact, organic differentiation was simultaneously the prerequisite and expression of all life, and no life-form could be proved that did not owe its existence to propagation by a parent.  What jubilation had greeted the first primal slime fished from the sea's deepest deeps--and what humiliation had followed.  It turned out that they had mistaken a precipitate of gypsum for protoplasm.  But to avoid one miracle (because it would be a miracle for life spontaneously to arise out of and return to the same stuff as inorganic matter), scientists had found it necessary to believe in another: archebiosis, that is, the slow formation of organic life from inorganic matter.  And so they went about inventing transitional and intermediate stages, assuming the existence of organisms lower than any known form, but which themselves were the result of even more primal attempts by nature to create life--attempts that no one would ever see, that were submicroscopic in size, and whose hypothesized formation pre supped a previous synthesis of protein. 
Mann goes on to answer the question of what is life poetically, as warmth produced by instability attempting to preserve form, the existence of that with no inherent ability to exist, and so on.  Mann needs no proof to support his answer, he can simply write it and it's there for as long as we can read.

Scientists, though, still struggle with their assumed transitional forms and submicroscopic particles. We claim not to believe in spontaneous generation, but we accept that it occurred (but only once!) in the primordial soup.  That starting event wasn't an act of God, as deists might claim, but the fluke (spontaneous, not pre-ordained) coming together of the right chemicals, perhaps plus some lightning bolts, to start the reaction that we know today as 'life'.

The idea that this occurred only once is preposterous.  It is far more likely that similar conditions in a similar span of time occurred trillions upon trillions of times within and among ponds, tides, shores, seas, rivers, lakes or wherever the magic soup occurred.  What we mean in science is that all of today's life came from one origin.  It leaves its trace of that single start-up.  More on that in a moment.

If we speculate on whether there are little green men (or even little red bacteria) on Mars, as a way of justifying costly tourist adventures there, then that's an acknowledgment that life arose by spontaneous combustion at least twice even within our own solar system!  (Unless of course we believe it was seeded on Earth by a meteor from Mars.) And if, as we discussed in previous posts on life in the universe, there are billions of habitable planets, even just thinking of earth-like life, then spontaneous generation of life is a downright everyday occurrence.  And if one thinks there are nearly infinitely many such planets, spontaneous generation is necessarily occurring somewhere, right this very minute (can you feel it?)!

So, it's not mysticism of any kind to argue for spontaneous generation.  And can we say that it is not still occurring, even here on earth?  One would have to rule out any possibility of the same chemical ingredients being present in right amounts anywhere on earth.  That seems at least somewhat unlikely (though, we think it is widely thought  that the actual origin of life was in an earth with oxygen-free atmosphere, so the question isn't so simple, and perhaps it's not occurring anywhere here any longer).

How can we as scientists deny, much less denigrate, Creationism if we then in our next breath, adopt  Darwin's final metaphor in the Origin, say that life was breathed into an otherwise inanimate earth?  The answer is simple, and relates to what is spontaneously being generated, and to the nature of life not just as a chemical phenomenon, but as a polymer phenomenon, as we described in earlier posts.  In part II of this short series, we'll elaborate.

Monday, January 23, 2012

Do we still not know what causes cancer? Part V. Simple complexity?

The insightful somatic mutational idea of Al Knudson's that retinoblastoma (RB) was due to two mutational hits, that accounted for the onset at or near birth, was based on the single vs multiple, unilateral vs bilateral nature of the primary tumors, and the difference between sporadic and familial cases.  Knudson's two-hit model originally (way back in 1971) was basically about two different genes needing to be mutated.  At the time we knew little about cell-to-cell signaling environments and the like, nor about the kinds of genes--related to basic cellular function--that might be responsible.  As it turned out, the RB story seemed to be one of two mutations--but in the different copies of the same gene, that when discovered was named RB1.  It turns out to be a tumor suppressor or 'anti-oncogene', one of the general classes of cancer-related mechanisms that research has identified.

As we said in the previous posts in this series, a consistent picture of the generic nature of genetic factors, based on cells' context-related behavior, seemed to have emerged from this insight.  It turned out that RB and perhaps a few other childhood tumors fit this simple one gene model.  There were some problems, in that mice engineered to be RB1-negative did not consistently have RB nor sometimes any serious abnormality.  And RB1 is expressed in many different cells, but had little direct relevance to other cancers (tumors didn't appear in childhood in other tissues).  Even so, again for whatever reason, this seemed to be a single-gene, single-tissue problem.  The idea could be that cancer is causally simple, and the job was just to identify the genes in each case (some of us were writing, even then, that the age pattern of other cancers suggested that they seemed to require 'hits' in multiple genes).

Cancer research following up on this and many other leads made great strides in many areas of basic cell biology and cellular communication--because cellular communication or cells sensing and responding to their environment is what complex organisms are all about. Cell-specific gene expression, signaling, and other aspects of cellular behavior were reflected in the abnormal cellular behavior of cancer.  RB1 inhibits cells from dividing until they are 'ready', meaning until other aspects of their behavior and responses have been set up (see Wikipedia: Retinoblastoma protein).

New light on an old story
But now even the RB story is turning out to be more subtle, and perhaps more complex than we had thought.  A new paper and commentary in Nature reports the story.  The question was how do RB1-negative cells end up being cancer cells?  Why does the absence of this gene matter?

The authors of the paper searched for other mutations in the genome in RB1 negative RB tumor cells, looking for evidence of a second 'hit'.  They did not find accumulating mutations.  In fact, they found that the retinoblastoma genome is more stable than that most other human cancers sequenced to date.  Rather than mutational or structural variations, they found that epigenetic changes were common.  These involve chemical modification of the nucleotides in the cells, rather than DNA sequence changes, the usual definition of mutation.  The changes include methylation of DNA that affects nearby gene expression and modification of the proteins that wrap up DNA in the nucleus and in turn are used to unwrap the DNA in areas where genes need to be expressed.

These modifications are driven by specific mechanisms that patrol DNA and, in ways not yet very well understood, modify it in chosen places.  But they do this systematically across the genome, making in a sense wholesale changes at a single go.  Those changes are somehow tissue context specific.  But the process does not require each site to be modified having to wait for a very rare mutational event. 

How RB1 protein affects cell cycle changes is not fully understood, but one thing that epigenetic changes can do is operate much faster than 'waiting' for a series of damaging DNA mutations to occur.  This works because epigenetic changes must occur all over the genome, since specific tissues use (or don't use) many different genes scattered across the chromosomes.  And tissue behavior can change, requiring different expression patterns: so the expression-regulating epigenetic changes have to be fast, modifiable, and reversible.  Which we know that they are.  Thus this is a plausible mechanism for the early onset of RB.  The authors identified a gene called SYK that may be particularly involved.

By contrast, for example, BRCA1 mutations damage DNA repair mechanisms, so that the person inheriting or incurring mutations in that gene becomes vulnerable to other mutations in her cells,  unfortunately including cancer-related mutations, that the cell can't detect and fix.  This shortens the average 'waiting' time for enough changes that a badly-responding breast cell divides out of normal contextual control.  BRCA1 related breast cancer is usually earlier than other cases.

Many changes all at once?
This may account for the early onset of the tumor when clearly just one aberrant gene doesn't alter so many aspects of the control of cell division and response.  Instead, the missing RB1 protein allows other processes involving many other genes to become deregulated--without having to be mutated themselves.  It would mean that RB as a disease is, like other cancers, the result of many changes in cell behavior, not just one.  In a sense that is reassuring, that we are correctly understanding that the mechanism of proper cooperation (to use MT's favorite term!) is required for appropriate cell behavior--appropriate in the sense that the pattern of cooperation evolved over time to produce the differentiated organ systems that we have in our bodies.

What does this say about Knudson's original two-hit model?  It was both right and wrong.  RB is a simple one-gene disease from the mutational view, but it is not a carcinogenic process that involves only one gene.   RB is a complex tumor, like other tumors, involving the actions of many genes, and their interactions with their contextual surroundings.  It is genetic in the sense that it involves aberrant use of many  genes, but it is contextual in that the genes are normal genes but mis-expressed in their context.  In truth, this is how all cancers are.  It just happens that this is driven by a single gene--or, of course, it could be that this works only in families transmitting otherwise unknown variation in genes that are vulnerable to these effects of the RB1 protein--that we don't yet know and would, like any GWAS problem, be challenging to discover.

A dangerous mix
Overall, what we see is a mix of somatic or inherited mutation, that unfortunately modifies a cell in nonmutational ways, that are genetic in the functional sense, yet are context-related because they  make the cell behave is if its context were different from the normal retinal context.  This is a mix of the two basic ideas of causation (called SMT and TOFT) that the BioEssays debate was about, and that originally triggered this series of commentaries.  In earlier installments in this series, we largely took sides, against the TOFT view, because it seemed to be in denial about the role that huge amounts of evidence provide for somatic mutations.  But as we've said in other parts of the series, no one can seriously argue that cancer is only genetic in the mutational sense, nor only involving somatic mutations.  The combination of causes is what is important and, we think, the age of onset pattern shows this.

But one of the reasons the genetic theory (including both somatic and inherited mutations) is so strongly supported by the evidence is that a great deal of evidence shows that tumors are, by and large, clones:  no matter how the tumor has spread in the body, all its millions of cells are descendants of a single 'transformed' cell.  There is evolution and genetic change among these cells, but they would share one or more changes that were there when that cell was transformed.  This is, we think, the typical finding.  There is, in fact, a new paper about the clonal nature of cancer in Nature.

By contrast, in any local cellular environment there are typically millions of cells, so that a screwy environment would misdirect responses in a great many cells, and the result would be a large number of primary tumors, and they would all look genetically normal. And they would have no reason to look so genetically abnormal as cancer cells.  Of course, abnormal cancer cells induce other perfectly normal cells, such as vessel-building cells, to provide nutrients, oxygen, and so on to the tumor cells.  So the tumor is much more than just the transformed cells.  The Nature review makes this clear, and that context is part of the story, which is related in a way to the TOFT theory, even if the article is from a cellular-genetic point of view..

Yes, we do know what causes cancer--generically.  It's about basic biology and the complex mix of causation, cooperation, and context that is the nature of life.  It's conceptually simple, but complex, like most of life, in the details of each instance.

Saturday, January 21, 2012

Give us a sporting chance!

Penn State is in the news everyday, and a long story in today's NY Times hammers on the drum of athletics out of control in universities.  It's possible, as a few lucky universities show, to have both: good athletics and good academics, but the greatest academic universities in the world don't, by and large. So it may be a cash cow but athletic departments aren't vital to good academics. But what, exactly, do administrators even mean when they utter the flash-word 'academics', and promise to keep them in balance with athletics, as our new president has said?  What are they themselves actually thinking?

Penn State's 108,000 seat Beaver Stadium
This is not so simple a matter, as the Times story points out.  Unfortunately, they take Penn State specifically to task for empty verbiage on this score.  When the promise of restoring 'balance' is mentioned, not a word is said about what that means.  Basically, so far, what it means here is paying a lot of money to Madison Avenue to create a new spin, perhaps some images on university web pages of students actually studying, or something hefty like that.

The truth is that SanduskyGate, which has been such a problem here at Penn State, is being treated as a problem for the athletic department.  There is heavy bemoaning of how our legendary coach Joe Paterno was forced to retire, with almost not a peep about the firing of the President.  Nobody gives a damn about him, it seems.  This safely sequesters the problem within the athletic department.  And here we're not referring to the incredibly tragic syzygy of awful events.  But the truth is much more profound than that.

We got into this mess, and other universities are vulnerable to the same thing, because as an institution we have been Republicanized: turned into a business to satisfy ourselves rather than our students, to raise money and take no chances.  We all know the grant system works that way--and by the way, this is not about Penn State but about all serious universities, of which we are clearly one.  We just had the bad luck to be embarrassed by it.

When we say we vow to restore a balance between athletics and academics, we de facto put them on the same scale, as equals!  That is preposterous!  And worse, of course we never say what 'academics' means.  That's because taking a stand on that is inconvenient; it takes guts and risk.  If we took it seriously, many students would not apply to come here--they even say in surveys that it's the athletics they come for.  That, in itself, is a preposterous big red flag.  And we're not alone, Paternoville or not.

We know very well that America's educational system, from K-12 through universities, is complacently and seriously dropping the ball.  Students aren't learning, aren't doing much homework, don't know how to find the library, and aren't nearly keeping up with the other countries' students with whom we compete for wealth and security.  As the Roman Emperor said, when the people are restless, give them bread and circuses.  To keep our student clientele, and though nobody says it out loud, what we provide are dumbed-down classes and spectator sports (and drinking venues).  To keep our tuition flowing so we can pay our faculty members and a horde of administrators quite handsomely, we have to avoid students dropping out.  We have to have looser admission standards, and admit thousands more customers than in the past (and claim that that's a good thing).  Don't scare them away from classes by using big words or insisting on attendance or giving bad grades or calling students on cheating! 

Science, our particular interest, to be done well requires properly skilled and trained professionals.  We're supposed to be providing them to society.  The current systematic backing down and easing up at universities--nationwide, not just here--is easy in the short-run but potentially devastating in the long run.  Broader scholarship than science, attitudes and nuances that make for more edifying lives and better citizens are similar.

However, how many administrators have what it takes, to take the risk with their trustees and donors, to  make real rather than cosmetic image-centered changes that will redress the problems?  How much we wish our leaders would do that!  Could it happen here, a place we care a lot about, now that we have been handed the opportunity, even if on a tarnished platter?

Leadership in such reform must be vigorous and persistent, because the problem is deep, systemic, and nationwide.  There will be resistance, even among faculty who won't want to change what or how often they teach or to demand more of better students, which demands more of themselves (ourselves). The news stories are all about a football coach and a boy getting shafted in a shower.  While the sexual abuse is the tragedy here, for universities the wider story is the economic bath we're all going to have to take if our nation doesn't get out the soap and clean things up.

Friday, January 20, 2012

Do we still not know what causes cancer? Part IV. The classic case returns....

We have had a series of posts (starting here) stimulated by a debate in BioEssays about whether one major idea about cancer, that it is due to somatic mutations (SMT), is correct, or whether a very different local-tissue-environment model (TOFT) explains the disease.

Given what it seems that we know, we should expect a spectrum of causation to apply, and we think that's what's been observed.  Clearly cancer is a disease of clonal expansion of cells, typically descendants of a single transformed founder cell.  The job of cells is to behave--express subsets of the genes in their genome--in ways that suit their local signaling (inter-cellular communication) environment. Gene expression is how this works, so clearly either mutant genes or mistaken interpretation of the environment, can trigger misbehavior.

First, the SMT, the idea that cancer is entirely due to somatic mutations, should be tempered, because it is manifestly clear that inherited mutations play a role, not just somatic mutations (that occur in body cells but were not inherited from the patient's parents).  As an overall generalization, cancers show mutations in many genes, but some of these have been inherited. Typically those are mutations that are 'recessive': if you get one 'bad' copy from one parent, but a good copy from your other parent, you're generally OK, unless you inherit deficient variants at other genes.  You get cancer if the good copy is somatically mutated in a cell, as well perhaps as other mutations in other genes or changes in the cellular environment.  Such genes are known as 'antioncogenes' or tumor supressor genes, because on their own they don't cause--and might function to hold back--abnormal cell behavior.  These are the main known genes in which inherited mutations lead to cancer. TP53, a gene that encodes the tumor-suppressor protein p53, is an example.

Oncogenes are those than can actively lead a cell astray, 'causing' cancer on their own (probably other factors  have to be present as well).  Mutations in these genes are rarely inherited, because the affected embryo doesn't make its 0th birthday.  If you suffer a somatic mutation in one of these (probably also if the cell has variants in additional genes, or the cell environment is changed somehow), you get cancer.

In either case, SMT argues that somatic mutations must contribute because, after all, you are born normal which means your inherited genotype didn't prevent proper tissue differentiation when you were an embryo. Debate was about how many or what or what types of genes were mutated somatically before someone got cancer. The age and rate of onset (age-specific 'hazard' function) seemed to reflect the number of changes that were needed to transform a cell, the number of cells at risk, and their cell-division rate.

The type of cancer that started us off on the path to the discovery of these aspects of cancer was the rare cancer of the retina (light perceiving layer inside the eye), retinoblastoma, or RB.  RB mainly occurs by birth or in early childhood.  It's rare, but one of the most stunning and influential discoveries--a true rather than hyped 'breakthrough'--was made in the early '70s by Al Knudson.  He observed that in sporadic RB only one eye was affected and usually with only one primary tumor.  But in the rare instance of inherited RB, both eyes were often affected, and by multiple independent tumors.

The idea struck Knudson that if some gene caused the tumor, then if no mutant copies of this gene were inherited, it would be very unlikely that any given retinal cell would be so unlucky as to experience mutations in both copies of the gene: hence sporadic RB is rare and unsually unilateral.  But if one bad copy were inherited, the fetus would only need to 'wait' for the other copy to be hit.  In the millions of newly forming retinal cells, it was reasonably likely that one or even many such cells would indeed be hit by another mutation.

The fact that RB occurred at birth rather than decades later, along with this idea about causation, suggested that there really was only one gene that needed to go bad.  By luck, a group involving Bob Ferrell, who was in Houston with Al Knudson (as was yours truly), discovered a chromosome change that was associated with RB in a family or two, and this led to the discovery of the gene, which was named RB1.

This opened many doors!  Knudson is widely honored, though he should in our opinion have been awarded a Nobel prize for his very insightful work (and he's a very nice person to boot!).  Anyway, to continue the story of the door he opened, soon other childhood tumors (esp. Wilm's tumor of the kidney) were found to have similar genetic epidemiology.  Then others, notably Bert Vogelstein and Ken Kinzler at Johns Hopkins, developed tests to see how often this phenomenon of somatic loss of a good copy of a tumor-suppressor gene occurred in people who had inherited one bad copy.  They found evidence that led to the discovery of other tumor suppressor genes, the most famous of which had to do with colon cancer (and the Tp53 gene that's involved in cell behavior).

Most tumors take decades to develop, even breast cancer in people inheriting mutations in BRCA genes (which is also in the suppressor category).  And this knitted tissue environmental factors (such as exposure to things including menstrual cycling and lactation that stimulated breast cell division) with genetic factors.  Each patient may have a unique set of many different mutations in other genes, some perhaps inherited others acquired somatically, and these were not terrible in themselves but carcinogenic in combination.  The idea of 'waiting' for these events to occur is strengthened by the discovery that BRCA works in a mutation-repair pathway.  So if you can't repair mutations, you're more likely to collect a bad set of them in some cell.

A generally consistent picture emerged, of complex, multifactorial genetic and histological processes that accounted for much of the epidemiology and genetics of cancer.  There are many aspects of this picture that require particular study and explanation.  It seemed that we had a pretty good understanding of the causal landscape, even if the specifics were complex or elusive.

But a new paper in Nature raises questions about even the simple RB model that are challenging to answer, in light of the above ideas.  That will be in Part V of this series on the causation of this dreaded disease--and what it tells us about basic cell biology.

Thursday, January 19, 2012

Probability does not exist! Part IV. Here's to your health!

Probability and unique events
Probability and statistics are very sophisticated, technical, often very mathematical sciences.  The field is basically about the frequency of occurrence of different possible outcomes of repeatable events.

When events can in fact be repeated, a typical use of statistical theory is to estimate the properties of what's being observed and assume, or believe, that these will pertain to future sets of similar observations.  If we know how a coin flipped in repeated observations in the past, we extrapolate that to future flips of that coin--or even to flips of other 'similar' coins.  If we observe thousands of soup cans coming off an assembly line, and know what fraction were filled slightly below specified weight, we can devise tests for efficiency of the machinery, or methods for detecting and rejecting under-weight cans.  And there are countless other situations in which repeatable events are clearly amenable to statistical decision-making.

When events cannot be or haven't been repeated, a common approach is to assume that they could be, and use the observed single-study data to infer the likely outcomes of possible repetitions.  As before, we extend our inference to to new situations in which similar conditions apply. In both truly and singular events there is similar reasoning, regardless of the details about which statisticians vigorously argue.

Everyone acknowledges that there is a fundamentally subjective element in making judgments, as we've described in the previous parts of this series of posts.  They are called, for example, significance tests from which one must choose a cutoff level or decision level.  But in well-controlled, relatively simple, especially repeatable situations, the theory at least provides some rigorous criteria for making the subjective choices.

The issues become much more serious and problematic when the situation we want to understand is either not replicable, not simple, not well understood, or in which even our idea of the situation is that the probabilities of different possible outcomes are very similar to each other.  Unfortunately, these are basic problems in much of biology.

Like dice, outcome probabilities are estimated from empirical data--past experience or experiments and finite (limited) samples.  Estimation is a mathematical procedure that depends on various assumptions and values, like averages of some measured trait, have measurement error and so on.  One might question these aspects of any study of the real world, but the issue for us here is that these estimates rest on some assumptions and are retrospective, because they are based on past experience.  But what we want those estimates for is to predict, that is to use them prospectively.

This is perhaps trivial for dice--we want to predict the probability of a 6 or 3 in the next roll, based on our observations of previous rolls.  We can be confident that the dice will 'behave' similarly.  Remarkably, we can also extrapolate this to other dice fresh from a new pack, that have never been rolled before, but only on the assumption that the new dice are just like the ones our estimates were derived from.  We can never be 100% sure, but it seems usually a safe bet--for coin-flips and dice.

Predicting disease outcomes
But this is far from the case in genetics, evolution, and epidemiology.  There, we know that no two people are genetically alike, no two have exactly the same environmental or lifestyle histories.  So that people are not exactly like dice.  Further, genes change (by mutation) and environments change, and these changes are inherently unpredictable as far as is known.  Thus, unlike dice, we cannot automatically extrapolate estimates from past experience such as genes or lifestyle factors and disease outcomes, to the future -- or from past observations to you.  That is, often or even typically, we simply cannot know how accurate an extrapolation will be, even if we completely believe in the estimated risks (probabilities) that we have obtained.

And, any risk estimation is inherently elusive anyway because people respond.  If you're told your risk of heart disease is 12%, that might make you feel pretty safe and you might stop exercising so much, or add more whipped cream to your cocoa, or take up smoking, but if you're told your risk is 30% you might do the opposite.  Plus, there's some thought that heart disease might have an infectious component, and that's never included in risk estimators, and is inherently stochastic anyway.  And, if there's a genetic component to risk, that can vary to the extent that many families might have an allele unique to them, which can't be included in the model because models are built on prior observations that won't apply to that family. 

A second issue is that even if the other things are orderly, in genetics and epidemiology and trying to understand natural selection and evolution, we are trying to understand outcomes whose respective probabilities are usually small and usually very similar.  As we've tried to show with the very similar (or identical?) probabilities of Heads vs Tails, or of 6 vs 3 on a die, this is very difficult even in highly controlled, easily repeatable situations.  But this simply is often not nearly the case in biology.

Here the risks of this vs that genotype, at many different genes simultaneously, are very indivdually small and similar, and that's why GWAS requires large samples, often gets apparently inconsistent results from study to study, accounts for small fractions of heritability (the estimated  overall genetic contribution).  This means that it is very difficult to identify genetic contributions that are statistically significant--that have strong enough effects to pass some subjective decision-making criterion.

This means it's very difficult to estimate a statistically reliable risk probability to persons based on their genotype, and certainly makes it difficult to assign a future risk. Or to know whether each person with that genotype has the same risk as the average for the group.  That is why many of us think that the current belief system, and that's what it is!, in personalized genomic medicine, is going to cost a lot for relatively low payoff, compared to other things that can be done with research funds---for example, to study traits that really are genetic: for which the risk of a given genotype is so great, relative to other genotypes, that we can reliably infer causation that is hugely important to individuals with the genotype, and for which the precision of risk estimates is not a big issue.

Probabilities and evolution
Similarly, in reconstructing evolution, if the differences among contemporary genotypes in terms of adaptive (reproductive) success are very similar, the actual success of the bearers of the different genotypes will be very similar, and these are probabilities (of reproduction or survival).  And if we want to estimate selection situations in the distant, unobserved past, from net results we see today, the problems are much more challenging even if we thoroughly believe in our theories about adaptive determinism or genetic control of traits.  Past adaptation also occurs, usually we think, very slowly over many many generations, making it very difficult to apply simple theoretical models.  Even to look for contemporary selection, other than in clear situations such as the evolution of antibiotic or pesticide resistance, is very challenging.  Selective differences must be judged only from data we have today, and directly observing causes for reproductive differences in the wild today is difficult and requires sample conditions rarely achievable.  So naturally it is hard to detect a pattern, hard to make causal assertions that are more than storytelling.

And, finally
We hope to have shown in this series of posts why we think we have to accept that 'probability' is an elusive notion, often fundamentally subjective and not different from 'belief'.  We set up criteria for believability (statistical significance cutoff values) upon which decisions--and in health, lives--depend.  The stability of the evidence and vagaries of cutoff-criteria, and our often reluctance to accept results we don't like (treating evidence that doesn't pass our cutoff criterion but is close to it as 'suggestive' of our idea rather than rejecting our idea), all conspire to raise very important issues for science.  The issues have to do with allocation of resources, egos, and other vested interests upon which serious decisions must be made.

In the end, causation must exist (we're not solopsists!), but randomness and probability may not exist other than in our heads.  The concept provides a tool for evaluating things that do exist, but in ways that are fundamentally subjective.  But we are in such a hurry in the system of science and its use that has evolved that we are not nearly humble enough in regard to what we know about what we don't know.   That is a fact that exists, whether probability does or not!

It is for these kinds of reasons that we feel research investment should concentrate on areas where the causal 'signal' is strong and basically unambiguous--traits and diseases for which a specific genetic causation is much more 'probable' than for the complex traits that are soaking up so many resources.  Even the 'simple' genetic traits, or simple cases of evolutionary signal, are hard enough to understand.

Wednesday, January 18, 2012

Probability does not exist. Part III. Making the call...

We continue a discussion of randomness, probability, and scientific inference.  We made some points in the first two installments about the elusive and subjective aspects of probability.  Here we'll ask a few similar kinds of questions, and then (finally!) get to the relevance for genetics and evolution and other areas like epidemiology.

What does it mean to say that a phenomenon is 'random'?  This is a rather subjective terms, but intuitively it means that nothing in a test or experiment affects the particular outcome.  If dice are thrown randomly, it means that nothing about the throw affects whether a 1 or 6 will come up.  More generally, dice throws would be said to be random events because each toss leaves each face equally likely to occur.  Equally likely is a rather circular term, but it implies again that each side comes up the same fraction of the time.

Many events are said to be random or probabilistic with the unstated assumption that the event is inherently random.  That there is no process that makes the outcome specifically predictable.  Quantum mechanics, to many people, are like that: the position of an electron around an atom is inherently probabilistic.  No matter how much information or perfect measurement we might have, the electron's position is only predictable in a probabilistic sense (forgive us, any physicist readers, if we're not well-enough informed to have described this properly!).

Other things are said to be 'random' in that while they might be deterministic, we simply can't tell the difference between that and a truly probabilistic process.  Dice rolling is generally viewed that way--as fundamentally random.  We saw in the previous installments that this can be modified in a way.  A six and a one may not have exactly the same probability of coming up on a given roll, but once we know their side-specific probability, the process is random relative to that.  If a 6 has prob. 0.168 and a 1 has prob 0.170 of coming up, those will be the fractions we'd observe, but cannot predict any more accurately than that.

Coin-flipping is a classic example of supposedly truly probabilistic events.  But is it?  Flipping coins lots of times never generates exactly 50% heads and 50% tails, the kind of discrepancy seen in dice.  But is the discrepancy we observe just experimental error of random processes, or is there a true bias--does one side 'really' have a higher chance of coming up roses?  Is coin-flipping a truly random process, or do we just not know enough to predict the outcome of a flip?

Here is a device developed a few years ago for a Stanford statistics professor named Persi Diaconis (who has special interests in the mathematics of gambling, magic, and things like that).  He has studied coin-flipping in practical as well as theoretical terms.  He has shown that if you set up the flip in the same way every time, you will get the same outcome every time -- that is, the outcome is entirely predictable.  Put this in other terms, as he has done in his paper on the subject, coin flipping is basically a standard physics phenomenon, that obeys the essentially deterministic laws of physics.  If you know all the relevant values about the coin, the flipping force and direct, the landing surface, and so on, the outcome is entirely predictable.

The reason outcomes seem 'random' is that there are so many things we don't know about a given flip, and so many differences from flip to flip, that we generally don't know enough to predict the outcome.  That is, they seem truly probabilistic.  But in a sense they are instead truly deterministic.

Diaconis and his co-authors analyzed the various factors, in classical physics terms, and to control for them and as we understand their result, they concluded that at least for their test coin, there was a 51% probability that the side that was up when flipped will come up at the end.  Flipping is somehow, and subtly, biased.

We make the call on coin-flipping at the beginning of a football game or to see who  pays for the next round of drinks, or who draws the short straw and has to do an unpleasant job.  We think of these as random.  But if we're skeptical, how do we make the call on that question itself?  Here, despite all of the above, and relevant to the entire nature of probabilistic-seeming events and understanding them, belief and subjectivity inevitably enter the room...whether or not their entrance is announced.

That's because at some point we have to decide whether the results (51% that the starting upside will be the ending upside) really do mean something in themselves, or are just the fluke results of a finite number of observations whose outcomes could be the way we see them 'just by chance'.  Even the latter phrase is circular and vague.  In the end, we decide what it takes for us to 'believe' one interpretation over another.  And there is no objective way to decide what we should believe: everyone has to make that call for him or herself!

If we see a situation in which different possible outcomes have very different probabilities--arise with very different fractions of the time--these issues may not arise.  We'd all agree on the general interpretation.  We share our beliefs.  Even with unique events, the assumption of probability that relates to the fraction of outcomes of each sort if the event could be repeated, is not a serious issue: results more or less bear out what we think we would see in repeated tests.  Or if we have seen a few repetitions of an event, we can be confident that we understand the relative probabilities of the outcomes.

But we've given a few examples of experiments to try to show how subtle and elusive concepts like randomness and probability are, even for the simplest and most controllable kinds of situations.  These are ones in which the probability differences among outcomes (heads vs tails, faces of dice) are very small (nearly 50% heads, 50% tails, 1/6 for each die face).

The reason for this is that in many situations in biology, including attempts to understand the relationship between genes and traits (e.g., GWAS, personalized medicine) or attempts to detect evidence of natural selection from gene sequences, the situation is more like dice:  things seem to be probabilistic--perhaps inherently so, and the probability differences between different outcomes, even according to our genetic and evolutionary theories, are very small.  Similar situations arise in epidemiology, as we've written often in MT, such as whether PSA testing improves prostate cancer outcomes, or vitamin supplements improve health, and so on.

That is, we're trying to detect small probabilistic needles in haystacks.  And, to a considerable extent, even according to the theory of those doing the studies and claiming to have found the evidence, the events are not repeatable.  In part IV of this series, we'll discuss these in more specific terms, in relation to the issues in the first 3 parts.

Tuesday, January 17, 2012

Probability does not exist. Part II. Some 'random' thoughts.

In Part I of this series we described the vagueness of the notion of probability.  It's an uncertain tangle of concepts that seem obvious but are almost impossible to define.  If you doubt that, go look for yourself on the web for terms like probability, chance, or random.

The terms are defined in circular ways (random means haphazard or due to chance) or in terms of events that were repeated, or that might be repeated in the future, or the fraction of those events with some particular property, or even of events that may not in fact occur or even be possible.  Or in terms of what might 'possibly' (another vague term) happen in the future.  Or how convinced we may be that it will happen.

Probability and statistics are at the very foundation of modern science.  But as specialists know and confess readily, the central terms are vague and in a formal sense, axiomatic.  You define a probability as a number between 0 and 1 that represents something related to the concepts mentioned in the previous paragraph.  An axiom is accepted and used, but not directly tested and need even not be a part of the real world.  2+2=4 is loaded with such kinds of assumptions.

Probability seems so deeply embedded, and just plain obvious, that it's hard to accept that its use and real-worldliness can be boiled down to beliefs or to something that we just take for granted rather than test.  Even something as simple as rolling dice shows the issues, and they're important because they are seen all over the place in human and evolutionary genetics.

From:  Ivar Peterson's Math Trek

Let's look at some tests done with dice.  Here are results from a web site tallying the rolling of 10,000 dice.  Now, the natural reaction is to assume that the spots on each face make no difference to whether it will end on top on a given roll.  Somehow we naturally then assume that in 10,000 roles we expect 1667 occurrences of each face. This was not always an obvious expectation, but it has been since WRF Weldon rolled 26,306 dice in 1894, which led to the still-current way we interpret such results.

Clearly, the expected result is not what happened!  Does this--the actual results, not anything 'theoretical'--then mean that the dice are biased in some way?  Nowadays we would all be unclear until we do some kind of statistical test.  Following what Karl Pearson developed from Weldon's experiments, we compare the above results with 1667 for each face and say yes, the two are different, but ask how different and whether it matters.  We use some subjective goodness-of-fit test cutoff level to evaluate the difference, such as are routine in science and taught in basic statistics courses.

If the subjective cutoff is exceeded, then we say that if our idea that, for whatever reason, each face should come up an equal number of times, the results are unusual enough that we doubt our idea.  A typical cutoff would be that if the difference would be as great as what we see in less than one experiment out of 20 experiments, we say our idea is not acceptable.  Note that this is purportedly a scientific approach, and science is supposed to be objective, but this is a wholly subjective choice of cutoff, and it assumes a lot of other things about the data (such as there was no cheating, each toss was done the same way, and so on).  Weldon's dice also seemed unfair, but in unclear ways, if one thinks of the possible reasons for unfairness.  They even wondered if one of the assistants doing the rolling might have done it differently.

This seems strange. We might decide that the dice are unfair in this subjective way, though that doesn't tell us how or why they're unfair.  But in another sense, the differences are numerically so small that we might say 'who cares?'  (Las Vegas gambling houses care!)

But notice something: on dice, the spots on opposite sides total to 7.  Thus one side has more spots than the opposing one.  For example, 1679 sixes vs 'only' 1654 ones.  This is true for all such pairs, even if the individual differences don't seem startlingly great.  But the above data suggest that since the spots are really dips in the surface of normal dice, they take some mass away so that the weight of the dice is shifted from dead center towards the heavier (fewer spot) side.  The more spots the lighter and the more often it comes up.  Bingo!  A physical explanation for an otherwise curious result!  (I understand that spots on Vegas dice are filled with black material of the same type as the rest of the die).

The significance test that led us to this decision does not imply that the next 10,000 throws of these same dice would come up the same, but the usual thing in science would be (1) stick to the fairness belief and ignore the result, assuming that the next result would be 'better', or (2) adjust the expectations from 1/6th for each side to these observed fractions, and then test the next experiment against these expectations.

Sounds good, and in fact someone has tried this kind of thing.  Here is a machine that mechanically flips dice (see Z. Labby, Chance, 2009).  The developer replicated Weldon's 26,306 throws of 12 dice.  No personal assistants, who might be subtly biased, involved!  The results are shown in this graph.  What you can see is that the previous 'pattern'  is not clear here.  It is ambiguous from the usual statistical testing whether these dice are biased or not--again, a subjective evaluation.  So what do we make of this?  We had a  physical model, but it wasn't borne out.  Was it wrong?

You can argue that the 3 experiments used different ways of tossing dice, or the dice were made  years apart and may be of different composition, and whatever else you can think of.  Or, you can say that this is a tempest in a teapot because these results are not very different from each other. 

Note here that there are ways to establish ranges around our observed results that represent what might have occurred  had the same dice been rolled the same number of times again (the brackets in the figure, for example, show this).  But one has to choose the limits subjectively.  The brackets would not be identical from experiment to experiment.

Even if you said that the results are not very different from each other, do you mean that they are not very different from 1/6 for all faces, or from the biased probabilities of the 10,000-roll experiment?  Or from some other type of bias?  Should you have a different amount of bias favoring the 6 from that of the 5 and the 4 (the lighter of their respective face-pairs)?

If this were something whose outcome affected you personally, you likely would say it doesn't matter, if you were playing Monopoly or shooting dice with friends.  But if you're the MGM Palace in Las Vegas, you would care much more, because there what counts, so to speak, is not the money made or lost by individuals but by your entire customer base. That can be a very big difference!

One last thought here.  The idea that we should expect each face to come up 1/6 of the time rests on the concept of 'randomness'.  But that is an idea so elusive one can ask what it actually means.  Normally the idea is that each die face is the same, and so there is 'no reason' any one should come up more often than another.  That is essentially unprovable and very likely untrue.  But at least, especially in Vegas dice with filled-in pips, the faces of a die are (if fairly manufactured etc. etc.!!) so similar that our intuitive concept is probably not so bad.  We were going to say that, after all, most such things do come up more or less as expected....but we hesitated, because we'd have expected that with dice, too!

The same problems and infuriating (or intriguing) issues arise in something so simple as coin-tossing and asking whether a coin is biased.  Normally we would consider it, like dice, to be a 'random' phenomenon and that's why heads and tails come up the same fraction of the time (if they do!).  This raises other fundamental questions, as we'll see in Part III.  There, we'll show how very relevant all of this is to human medical genetics, studies like GWAS, and to the inferences we make about evolution.

Monday, January 16, 2012

Changing the goal posts: heritability lost and found

We interrupt our series on Probability and its meaning, for a post that we've been asked to write, related to a new paper on gene hunting that got some press last week, and will be stirring up controversy (and naturally, we can't resist including our usual editorializing, for better or worse):

Making complexity simple (again)?
Every age and every profession has its PT Barnums.  They're the slick-talking, fast-moving guys who will say anything to draw customers into the show they're running.  Truth, if it even exists other than ambiguously, is secondary in many ways to closing the deal.

One tactic that the pitchmen use in fields like politics is to change definitions so that problems never get 'solved' (that is, there is always something to keep you in office or to keep levying taxes, or to keep you afraid of some enemy or other).  This is a way of making the same facts serve new interests.

Science is rife with these kinds of self-interested maneuvers.  Changing the goalposts in genetics means redefining the objectives or the criteria for pushing ahead even in the face of contrary evidence.  This is a system we've built, step by step, once government funding largesse started flowing some time during the Cold War.  And today, in genetics, which plays on fear of death just as much as preachers do, we have to keep passing the plate.  Yet science is supposed to be objective and 'evidence based'.  So we have to change the goalposts to keep the game from ending.  In this case, there is a recent paper, with promise of more to come, by Eric Lander and colleagues (Zuk et al.).  Because of his prominence, skill, and salesmanship this will of course get a lot of attention.

The paper discusses at least one reason why GWAS have not been very good at accounting for heritability (something we ourselves have commented on in many posts).  Some, who are critical, say that this paper finally shows that GWAS and related big-scale approaches are proliferating even though they have themselves shown that they've reached diminishing returns.  Here's an example.  Of course there's the resistance that says no, Bravo! to the new paper, which shows that we're just getting started!

Naturally, everyone shares an interest in saying that to show their favorite view we need mega-GWAS, Biobank, gobs of wholegenome sequence, or other similar open-ended approaches, and whether this will lead to the ultimate small scale objective of personalized 'genomic' medicine.  Far too many vested interests are at play and, indeed, training in 'grantsmanship' and the whole research culture is about manipulating the system to get, keep, and increase funding. 

Zuk et al. ask why GWAS have failed to account for the heritability of so many traits, that is, to explain the correlation in risk among family members that reflects genetic effects.  The subject is complex, but here we can just say that if each gene adds a dose of effect to a trait, like nibbles on a given side of the caterpillar's mushroom added to Alice's stature, then even if the effect of nibbles is very small, if we sample enough mushrooms we can identify all of the effects.  Then, knowing them, we can tell which nibbles a given person has made, and hence predict his stature:  Voila!  personalized medicine!

Yet it hasn't worked that way.  Most heritability remains unaccounted for despite already very large studies.  Hence the demand for ever larger studies.  A glib commentary in Nature a few years ago coined the term 'hidden heritability' and made the search to find it akin to Sherlock Holmes' search for Moriarty.  That was a fantastic, if anti-science, marketing ploy on Nature's part, since it fed an ever-increasing demand for funds for genomic scavenger hunting....and that's good for the science journal business!

But the search for this hidden treasures has been frustrating, and Zuk et al. claim they now know that the search is in vain, and they provide a very sophisticated mathematical account of the reason why.  It is due to gene interactions, or 'epistasis'.  That means that a large part of the correlation among relatives can't be found by looking only for additive effects.  Here's roughly a basic underlying concept:

If trait T, such as stature or insulin levels (or their disease-risk consequences) is due to the effects of factor A plus those of factor B, then we can write

T = A + B

If your genotype includes a variant A-gene that gives you an additional level of factor A, then for you

T = A + A + B,   or 2A + B.

But if the factors interact, say in a multiplicative way, then

T = AxB

and if that's what's going on, and your A-gene genotype adds a second dose of A, your trait is

T = (2A) x B =  2AB

So, let's say a normal person has A=3 trait units and B=4 trait units.  In the additive case that person's trait would be A+B=7.  And if you have a mutation that doubles your A-dose, then your genotype makes you 2A+B=10 for your trait value.  But in the epistasis case, your trait would actually be 24.  So we expect you to have trait value 10, and conclude that more than half your trait value is unexplained.

Functional interaction
Nobody disputes a central fact in the Zuk et al. argument.  Life works by interactions among genes.  These are functional interactions in systems called 'networks' and other sorts of molecular interactions.  One molecule doesn't do anything by itself, nor does one gene as a rule.  Here, each gene-related component is subject to variation by mutation, and that will be inherited (its effects contributing to heritability).  So it is obvious from a cell biology point of view that single-factor explanations are not going to tell the whole story. But the fact of multiple factors doesn't tell the story we're interested in predicting states among variable traits.  That involves a different kind of interaction.

Quantitative interaction
If the true-fact is that biological traits are the result of functional interactions, what epidemiological risk estimation is about is not a list of pathways but the effects of variation in the pathways. When factors interact in a non-additive way, their net result is estimated from sample data using statistical techniques.  The A B example above showed conceptually how they work.  The additive contributions of variants in factor A are estimated from samples that compare those with and those without the variant in question.  You can estimate each factor's effects independently in this way and add up the estimates.

But if they interact, then in essence you have to have an additional estimate to make, of the average trait value in groups of people with each combination of the variants at the interacting factors.

Not only does this require more data, it won't show up in GWAS types of case-control or similar data.  You need to look in other ways.

Zuk et al. address this.  They build their idea that much of the observed heritability is estimated on a purely additive model, and yet at least some factors may be what in standard biochemical terms is known as 'rate limiting' effects.  At some level of concentration of such factors, they or what they interact with no longer works the same way if it works at all.  The authors outline a model which, under various assumptions about how many steps are rate-limiting such that variants in those steps define measures of heritability, might begin to explain familial correlations not accounted for by current additive effects.

It is already nigh impossible to get stable estimates of hundreds of additive effects, mostly very small (see our current series of posts on Probability does not exist!).  It's one thing to estimate the effects of, say, 100 additively contributing genes. Variants will be many in each, variable in their frequencies among samples.  If purely additive, the context doesn't matter: in each population you can estimate each factor's effect and add 'em up to get a given person's risk.  But if context matters, that is, if the effect of one factor depends on the specific variants in the rest of the genome (forgetting environmental effects!) then it's quite another to estimate those interactions.  Roughly, if 100 genes interact in pairwise fashion (2-way interactions like AxB only), that means 10,000 interaction effects to estimate. Zuk et al. certainly acknowledge this problem clearly.  But the authors suggest kinds of data on relatives of various degrees that might be practicably collected and could reveal discrepancies from expectations under additive models, and account for more or all of the heritability.

Zuk et al. promise that if we study 'isolated' populations we'll have a shot at the answer!  This is not new, and indeed studies in Finland and Iceland led a previous charge for similar reasons.  Perhaps it is a good idea....and the authors provide tests that could be done if there were adequate data collected.  It will be done and will expend more millions of research dollars in the process.  But, if complexity is real, the most we'll get is a few hits and a few weak statistical signals.  But we're in that place already, so in that sense this is another way of changing the goalposts, because we did not reap bonanza from those studies.

The answer
Like most such papers, Zuk et al. make gobs of assumptions about the model, the data, and the underlying basis of dichotomous disease (present or absent).  Facing such complex problems it's hard or impossible not to make simplifying or exemplifying assumptions.  As usual, if one probes these assumptions, there will be additional sources of variation and uncertainty that are being ignored or that must be estimated from data, so that even the rosy answers suggested by the authors, which are far from promising a complete understanding, will be overstated (and that is the clear-cut history of the senior author, and most of his peers in the profession, including Francis Collins).

The actual answer is well known, even if it's resisted because it's not very convenient: life is a mixture, or spectrum, of all of these kinds of components.  We know that additive models work very well in many domains, such as agricultural and experimental breeding (artificial selection), and that as GWAS sample sizes have increased steadily they have steadily been identifying more contributing genes.   That is, we have not plateaued to a point that bigger samples will not add more genes, the remaining recalcitrant effect due to interaction.  We think even the authors acknowledge that the interactions may comprise sets of individually weak contributors.

Further, because most variants in our population are in fact, and indisputably, rare to very rare, they form a large aggregate of potentially contributing genes that will vary from sample to sample and population to population.  This is, really, a fact of life.

Networks, the  sugar plum fairies of promised genomic medical miracles, involve tens of genes, many with multi-way interactions, like AxBxC. And what of higher-order interactions such as the square of one or more factor levels?  One might as well count stars in heaven as attempt to collect accurate data from the entire human species in order to get enough data to estimate these effects.   And that, of course, is foolish for many reasons, not least being that environmental factors change and vary and heritability is a measure of genetic relative to environmental effects.

Zuk et al. are promising a series of papers along this track, and have coined a new name for their idea (a standard marketing ploy). We'll be hearing a lot of me-tooism, users avidly diving into the LP (limiting pathway) model.  That certainly doesn't make the model wrong, but it does affect where the goalposts are. We're hopefully not hypocrites: we have our own simulation program, called ForSim (freely available to others) by which some of these things could be simulated, and we may do that.

Nobody can seriously question that context is very important, and that includes various kinds of interactions.  But the issue is not just what the mix of types of contribution are, how stable, how variable among samples, and so on.  Even if Zuk et al. are materially correct, it doesn't erase the problematic nature of trying to estimate, much less generally to do much about, the joint effects of the many genes, in their tens or hundreds, whose variation contributes to a trait of interest.

"Discovery efforts should continue vigorously"
We ourselves are far from qualified to find technical fault with the new model, if there is any.  We doubt there is.  But the point is not that this new paper is flim-flam, even if it simplifies and makes many assumptions that could be viewed as perhaps-necessary legerdemain, given the situation's complexity.  Or, perhaps more clearly, red-herrings to distract attention from the real point, which is  whether changing the goalposts in this kind of way changes the game.

One can ask--should ask--whether regardless of interaction or additivity, it's worth trying to document them, or whether Francis Collins' insistence on luxury medicine (personalized prediction of weak effects with lifelong treatment mainly available to paying customers) is a realizable goal.  The same funds could, after all, be spent in other ways on indisputably stronger and simpler genetic problems, that could be far more directly and sooner relevant to the society that's paying the bill.

Arguing either/or (additive or non-additive) and attempting to relate that to the desirability of keeping the Big Study funds flowing is a carnival barker activity.  The authors at one point subtly make the anti-Collinsian but obvious point that personalized gene-based prediction is generally going to be a bust.  But then they argue let's plow ahead to discover pathways. Let's have our goalposts everywhere at once!  There are other, better, logistically easier and probably less costly ways to find networks and if there aren't already, there ought to be research invested in figuring them out (e.g., in cell cultures).  Epidemiological studies are expensive and of low payoff in this kind of context.

As the authors clearly say: discovery efforts should continue vigorously" despite their points, acknowledging in fact and cleverly hedging all bets, that many variants remain to be discovered by current approaches.  This is a fair-grounds where PT Barnums thrive.  It keeps their particular circus's seats filled.  But that doesn't make it the best science in the public interest.