Thursday, November 7, 2013

The dark arts of statistical genomics

Whereof one cannot speak, thereof one must be silent” - Wittgenstein

That’s a maxim to live by, or certainly to blog by, but I am about to break it. Most of the time I try to write about things I feel I have some understanding of (rightly or wrongly) or at least an informed opinion on. But I am writing this post from a position of ignorance and confusion.

I want to discuss a fairly esoteric and technical statistical method recently applied in human genetics, which has become quite influential. The results from recent studies using this approach have a direct bearing on an important question – the genetic architecture of complex diseases, such as schizophrenia and autism. And that, in turn, dramatically affects how we conceptualise these disorders. But this discussion will also touch on a much wider social issue in science, which is how highly specialised statistical claims are accepted (or not) by biologists or clinicians, the vast majority of whom are unable to evaluate the methodology.

Speak for yourself, you say! Well, that is exactly what I am doing.
The technique in question is known as Genome-wide Complex Trait Analysis (or GCTA). It is based on methods developed in animal breeding, which are designed to measure the “breeding quality” of an animal using genetic markers, without necessarily knowing which markers are really linked to the trait(s) in question. The method simply uses molecular markers across the genome to determine how closely an animal is related to some other animals with desirable traits. Its application has led to huge improvements in the speed and efficacy of selection for a wide range of traits, such as milk yield in dairy cows.   

GCTA has recently been applied in human genetics in an innovative way to explore the genetic architecture of various traits or common diseases. The term genetic architecture refers to the type and pattern of genetic variation that affects a trait or a disease across a population. For example, some diseases are caused by mutations in a single gene, like cystic fibrosis. Others are caused by mutations in any of a large number of different genes, like congenital deafness, intellectual disability, retinitis pigmentosa and many others. In these cases, each such mutation is typically very rare – the prevalence of the disease depends on how many genes can be mutated to cause it.

For common disorders, like heart disease, diabetes, autism and schizophrenia, this model of causality by rare, single mutations has been questioned, mainly because such mutations have been hard to find. An alternative model is that those disorders arise due to the inheritance of many risk variants that are actually common in the population, with the idea that it takes a large number of them to push an individual over a threshold of burden into a disease state. Under this model, we would all carry many such risk variants, but people with disease would carry more of them.
That idea can be tested in genome-wideassociation studies (GWAS). These use molecular methods to look at many, many sites in the genome where the DNA code is variable (it might be an “A” 30% of the time and a “T” 70% of the time). The vast majority of such sites (known as single-nucleotide polymorphisms or SNPs) are not expected to be involved in risk for the disease, but, if one of the two possible variants at that position is associated with an increased risk for the disease, then you would expect to see an increased frequency of that variant (say the “A” version) in a cohort of people affected by the disease (cases) versus the frequency in the general population (controls). So, if you look across the whole genome for sites where such frequencies differ between cases and controls you can pick out risk variants (in the example above, you might see that the “A” version is seen in 33% of cases versus 30% of controls). Since the effect of any one risk variant is very small by itself, you need very large samples to detect statistically significant signals of a real (but small) difference in frequency between cases and controls, amidst all the noise.  

GWAS have been quite successful in identifying many variants showing a statistical association with various diseases. Typically, each one has a tiny statistical effect on risk by itself, but the idea is that collectively they increase risk a lot. But how much is a lot? That is a key question in the field right now. Perhaps the aggregate effects of common risk variants explain all or the majority of variance in the population in who develops the disease. If that is the case then we should invest more efforts into finding more of them and figuring out the mechanisms underlying their effects.

Alternatively, maybe they play only a minor role in susceptibility to such conditions. For example, the genetic background of such variants might modify the risk of disease but only in persons who inherit a rare, and seriously deleterious mutation. This modifying mechanism might explain some of the variance in the population in who does and does not develop that disease, but it would suggest we should focus more attention on finding those rare mutations than on the modifying genetic background. 

For most disorders studied so far by GWAS, the amount of variance collectively explained by the currently identified common risk variants is quite small, typically on the order of a few percent of the total variance.
But that doesn’t really put a limit on how much of an effect all the putative risk variants could have, because we don’t know how many there are. If there is a huge number of sites where one of the versions increases risk very, very slightly (infinitesimally), then it would require really vast samples to find them all. Is it worth the effort and the expense to try and do that? Or should we be happy with the low-hanging fruit and invest more in finding rare mutations? 

This is where GCTA analyses come in. The idea here is to estimate the total contribution of common risk variants in the population to determining who develops a disease, without necessarily having to identify them all individually first. The basic premise of GCTA analyses is to not worry about picking up the signatures of individual SNPs, but instead to use all the SNPs analysed to simply measure relatedness among people in your study population. Then you can compare that index of (distant) relatedness to an index of phenotypic similarity. For a trait like height, that will be a correlation between two continuous measures. For diseases, however, the phenotypic measure is categorical – you either have been diagnosed with it or you haven’t.

So, for diseases, what you do is take a large cohort of affected cases and a large cohort of unaffected controls and analyse the degree of (distant) genetic relatedness among and between each set. What you are looking for is a signal of greater relatedness among cases than between cases and controls – this is an indication that liability to the disease is: (i) genetic, and (ii) affected by variants that are shared across (very) distant relatives.
The logic here is an inversion of the normal process for estimating heritability, where you take people with a certain degree of genetic relatedness (say monozygotic or dizygotic twins, siblings, parents, etc.) and analyse how phenotypically similar they are (what proportion of them have the disease, given a certain degree of relatedness to someone with the disease). For common disorders like autism and schizophrenia, the proportion of monozygotic twins who have the disease if their co-twin does is much higher than for dizygotic twins. The difference between these rates can be used to estimate how much genetic differences contribute to the disease (the heritability).

With GCTA, you do the opposite – you take people with a certain degree of phenotypic similarity (they either are or are not diagnosed with a disease) and then analyse how genetically similar they are.

If a disorder were completely caused by rare, recent mutations, which would be highly unlikely to be shared between distant relatives, then cases with the disease should not be any more closely related to each other than controls are. The most dramatic examples of that would be cases where the disease is caused by de novo mutations, which are not even shared with close relatives (as in Down syndrome). If, on the other hand, the disease is caused by the effects of many common, ancient variants that float through the population, then enrichment for such variants should be heritable, possibly even across distant degrees of relatedness. In that situation, cases will have a more similar SNP profile than controls do, on average.

Now, say you do see some such signal of increased average genetic relatedness among cases. What can you do with that finding? This is where the tricky mathematics comes in and where the method becomes opaque to me. The idea is that the precise quantitative value of the increase in average relatedness among cases compared to that among controls can be extrapolated to tell you how much of the heritability of the disorder is attributable to common variants. How this is achieved with such specificity eludes me.

Let’s consider how this has been done for schizophrenia. A 2012 study by Lee and colleagues analysed multiple cohorts of cases with schizophrenia and controls, from various countries. These had all been genotyped for over 900,000 SNPs in a previous GWAS, which hadn’t been able to identify many individually associated SNPs.

Each person’s SNP profile was compared to each other person’s profile (within and between cohorts), generating a huge matrix. The mean genetic similarity was then computed among all pairs of cases and among all pairs of controls. Though these are the actual main results – the raw findings – of the paper, they are remarkably not presented in the paper. Instead, the results section reads, rather curtly:

Using a linear mixed model (see Online Methods), we estimated the proportion of variance in liability to schizophrenia explained by SNPs (h2) in each of these three independent data subsets. … The individual estimates of h2 for the ISC and MGS subsets and for other samples from the PGC-SCZ were each greater than the estimate from the total com­bined PGC-SCZ sample of h2 = 23% (s.e. = 1%)

So, some data we are not shown (the crucial data) are fed into a model and out pops a number and a strongly worded conclusion: 23% of the variance in the trait is tagged by common SNPs, mostly functionally attributable to common variants*. *[See important clarification in the comments below - it is really the entire genetic matrix that is fed into the models, not just the mean relatedness as I suggested here. Conceptually, the effect is still driven by the degree of increased genetic similarity amongst cases, however]. This number has already become widely cited in the field and used as justification for continued investment in GWAS to find more and more of these supposed common variants of ever-decreasing effect.

Now I’m not saying that that number is not accurate but I think we are right to ask whether it should simply be taken as an established fact. This is especially so given the history of how similar claims have been uncritically accepted in this field. 

In the early 1990s, a couple of papers came out that supposedly proved, or at least were read as proving, that schizophrenia could not be caused by single mutations. Everyone knew it was obviously not always caused by mutations in one specific gene, in the way that cystic fibrosis is. But these papers went further and rejected the model of genetic heterogeneity that is characteristic of things like inherited deafness and retinitis pigmentosa. This was based on a combination of arguments and statistical modelling.

The arguments were that if schizophrenia were caused by single mutations, they should have been found by the extensive linkage analyses that had already been carried out in the field. If there were a handful of such genes, then this criticism would have been valid, but if that number were very large then one would not expect consistent linkage patterns across different families. Indeed, the way these studies were carried out – by combining multiple families – would virtually ensure you would not find anything. The idea that the disease could be caused by mutations in any one of a very large number (perhaps hundreds) of different genes was, however, rejected out of hand as inherently implausible. [See here for a discussion of why a phenotype like that characterising schizophrenia might actually be a common outcome].
The statistical modelling was based on a set of numbers – the relative risk of disease to various family members of people with schizophrenia. Classic studies found that monozygotic twins of schizophrenia cases had a 48% chance (frequency) of having that diagnosis themselves. For dizygotic twins, the frequency was 17%. Siblings came in about 10%, half-sibs about 6%, first cousins about 2%. These figures compare with the population frequency of ~1%.

The statistical modelling inferred that this pattern of risk, which decreases at a faster than linear pace with respect to the degree of genetic relatedness, was inconsistent with the condition arising due to single mutations. By contrast, these data were shown to be consistent with an oligogenic or polygenic architecture in affected individuals.

There was however, a crucial (and rather weird) assumption – that singly causal mutations would all have a dominant mode of inheritance. Under that model, risk would decrease linearly with distance of relatedness, as it would be just one copy of the mutation being inherited. This contrasts with recessive modes requiring inheritance of two copies of the mutation, where risk to distant relatives drops dramatically. There was also an important assumption of negligible contribution from de novo mutations. As it happens, it is trivial to come up with some division of cases into dominant, recessive and de novo modes of inheritance that collectively generate a pattern of relative risks similar to observed. (Examples of all such modes of inheritance have now been identified). Indeed, there is an infinite number of ways to set the (many) relevant parameters in order to generate the observed distribution of relative risks. It is impossible to infer backwards what the actual parameters are. Not merely difficult or tricky or complex – impossible.

Despite these limitations, these papers became hugely influential. The conclusion – that schizophrenia could not be caused by mutations in (many different) single genes – became taken as a proven fact in the field. The corollary – that it must be caused instead by combinations of common variants – was similarly embraced as having been conclusively demonstrated.

This highlights an interesting but also troubling cultural aspect of science – that some claims are based on methodology that many of the people in the field cannot evaluate. This is especially true for highly mathematical methods, which most biologists and psychiatrists are ill equipped to judge. If the authors of such claims are generally respected then many people will be happy to take them at their word. In this case, these papers were highly cited, spreading the message beyond those who actually read the papers in any detail.

In retrospect, these conclusions are fatally undermined not by the mathematics of the models themselves but by the simplistic assumptions on which they are based. With that precedent in mind, let’s return to the GCTA analyses and the strong claims derived from them.

Before considering how the statistical modelling works (I don’t know) and the assumptions underlying it (we’ll discuss these), it’s worth asking what the raw findings actually look like.

While the numbers are not provided in this paper (not even in the extensive supplemental information), we can look at similar data from a study by the same authors, using cohorts for several other diseases (Crohn’s disease, bipolar disorder and type 1 diabetes).

Those numbers are a measure of mean genetic similarity (i) among cases, (ii) among controls and (iii) between cases and controls. The important finding is that the mean similarity among cases or among controls is (very, very slightly) greater than between cases and controls. All the conclusions rest on this primary finding. Because the sample sizes are fairly large and especially because all pairwise comparisons are used to derive these figures, this result is highly statistically significant. But what does it mean?

The authors remove any persons who are third cousins or closer, so we are dealing with very distant degrees of genetic relatedness in our matrix. One problem with looking just at the mean level of similarity between all pairs is it tells us nothing about the pattern of relatedness in that sample.

Is the small increase in mean relatedness driven by an increase in relatedness of just some of the pairs (equivalent to an excess of fourth or fifth cousins) or is it spread across all of them? Is there any evidence of clustering of multiple individuals into subpopulations or clans? Does the similarity represent “identity by descent” or “identity by state”? The former derives from real genealogical relatedness while the latter could signal genetic similarity due to chance inheritance of a similar profile of common variants – presumably enriched in cases by those variants causing disease. (That is of course what GWAS look for).  

If the genetic similarity represents real, but distant relatedness, then how is this genetic similarity distributed across the genome, between any two pairs? The expectation is that it would be present mainly in just one or two genomic segments that happen to have been passed down to both people from their distant common ancestor. However, that is likely to track a slight increase in identity by state as well, due to subtle population/deep pedigree structure. Graham Coop put it this way in an email to me: “Pairs of individuals with subtly higher IBS genome-wide are slightly more related to each other, and so slightly more likely to share long blocks of IBD.”

If we are really dealing with members of a huge extended pedigree (with many sub-pedigrees within it) – which is essentially what the human population is – then increased phenotypic similarity could in theory be due to either common or rare variants shared between distant relatives. (They would be different rare variants in different pairs). 

So, overall, it’s very unclear (to me at least) what is driving this tiny increase in mean genetic similarity among cases. It certainly seems like there is a lot more information in those matrices of relatedness (or in the data used to generate them) than is actually used – information that may be very relevant to interpreting what this effect means.

Nevertheless, this figure of slightly increased mean genetic similarity can be fed into models to extrapolate the heritability explained – i.e., how much of the genetic effects on predisposition to this disease can be tracked by that distant relatedness. I don’t know how this model works, mathematically speaking. But there are a number of assumptions that go into it that are interesting to consider.

First, the most obvious explanation for an increased mean genetic similarity among cases is that they are drawn from a slightly different sub-population than controls. This kind of cryptic population stratification is impossible to exclude in ascertainment methods and instead must be mathematically “corrected for”. So, we can ask, is this correction being applied appropriately? Maybe, maybe not – there certainly is not universal agreement among the Illuminati on how this kind of correction should be implemented or how successfully it can account for cryptic stratification.

The usual approach is to apply principal components analysis to look for global trends that differentiate the genetic profiles of cases and controls and to exclude those effects from the models interpreting real heritability effects. Lee and colleagues go to great lengths to assure us that these effects have been controlled for properly, excluding up to 20 components. Not everyone agrees that these approaches are sufficient, however.
Another major complication is that the relative number of cases and controls analysed does not reflect the prevalence of the disease in the population. In these studies, there were about equal numbers of each in fact, versus a 1:100 ratio of cases to controls in the general population for disorders like schizophrenia or autism. Does this skewed sampling affect the results? One can certainly see how it might. If you are looking to measure an effect where, say, the fifth cousin of someone with schizophrenia is very, very slightly more likely to have schizophrenia than an unrelated person, then ideally you should sample all the people in the population who are fifth cousins and see how many of them have schizophrenia. (This effect is expected to be almost negligible, in fact. We already know that even first cousins have only a modestly increased risk of 2%, from a population baseline of 1%. So going to fifth cousins, the expected effect size would likely only be around 1.0-something, if it exists at all).

You’d need to sample an awful lot of people at that degree of relatedness to detect such an effect, if indeed it exists at all. GCTA analyses work in the opposite direction, but are still trying to detect that tiny effect. But if you start with a huge excess of people with schizophrenia in your sample, then you may be missing all the people with similar degrees of relatedness who did not develop the disease. This could certainly bias your impression of the effect of genetic relatedness across this distance.

Lee and colleagues raise this issue and spend a good deal of time developing new methods to statistically take it into account and correct for it. Again, I cannot evaluate whether their methods really accomplish that goal. Generally speaking, if you have to go to great lengths to develop a novel statistical correction for some inherent bias in your data, then some reservations seem warranted.

So, it seems quite possible, in the first instance, that the signal detected in these analyses is an artefact of cryptic population substructure or ascertainment. But even if it we take it as real, it is far from straightforward to divine what it means.

The model used to extrapolate heritability explained has a number of other assumptions. First, is that all genetic interactions are additive in nature. [See here for arguments why that is unlikely to reflect biological reality]. Second, it assumes that the relationship between genetic relatedness and phenotypic similarity is linear and can be extrapolated across the entire range of relatedness. At least, all you are supposedly measuring is the tiny effect at extremely low genetic relatedness – can this really be extrapolated to effects at close relatedness? We’ve already seen that this relationship is not linear as you go from twins to siblings to first cousins – those were the data used to argue for a polygenic architecture in the first place.

This brings us to the final assumption implicit in the mathematical modelling – that the observed highly discontinuous distribution of risk to schizophrenia actually reflects a quantitative trait that is continuously (and normally) distributed across the whole population. A little sleight of hand can convert this continuous distribution of “liability” into a discontinuous distribution of cases and controls, by invoking a threshold, above which disease arises. While genetic effects are modelled as exclusively linear on the liability scale, the supposed threshold actually represents a sudden explosion of epistasis. With 1,000 risk variants you’re okay, but with say 1,010 or 1,020 you develop disease. That’s non-linearity for free and I’m not buying it.

I also don’t buy an even more fundamental assumption – that the diagnostic category we call “schizophrenia” is a unitary condition that defines a singular and valid biological phenotype with a common etiology. Of course we know it isn’t – it is a diagnosis of exclusion. It simply groups patients together based on a similar profile of superficial symptoms, but does not actually imply they all suffer from the same condition. It is a place-holder, a catch-all category of convenience until more information lets us segregate patients by causes. So, the very definition of cases as a singular phenotypic category is highly questionable.

Okay, that felt good.

But still, having gotten those concerns off my chest, I am not saying that the conclusions drawn from the GCTA analyses of disorders like schizophrenia and autism are not valid. As I’ve said repeatedly here, I am not qualified to evaluate the statistical methodology. I do question the assumptions that go into them, but perhaps all those reservations can be addressed. More broadly, I question the easy acceptance in the field of these results as facts, as opposed to the provisional outcome of arcane statistical exercises, the validity of which remains to be established. 

Facts are stubborn things, but statistics are pliable.” – Mark Twain


Sunday, November 3, 2013

Popping the hood on synaesthesia – what’s going on in there?,333/synesthesia-colourful-numbers-tasty-music-loud-food,1560
-->Synaesthesia – a “mixing of the senses” – was a popular scientific topic in the late 19th century, but fell out of favour during the mid-20th century, mainly due to the influence of behaviorism, which held that subjective experience was not a suitable subject for serious science. The start of this century has seen resurgence in interest in the topic, partly fuelled by the hope that neuroimaging would provide objective measures of what is happening in the brains of people during synaesthetic experiences.

We (Erik O’Hanlon, Fiona Newell and myself) have recently published our own neuroimaging study of synaesthesia, combining structural and functional analyses. Some of what follows is pulled from that paper, which contains references to the many studies cited below. Many of the ideas below are also discussed in a chapter I wrote for the new Oxford Handbook of Synaesthesia: Synaesthesia and cortical connectivity – a neurodevelopmental perspective.

The term synaesthesia refers both to the experience of some kind of cross-activation from one sense to another (but see more below) and to the condition of being prone to such experiences. It can be caused acutely in some people by drugs like LSD or psilocybin, which can famously induce visual experiences in response to music. It can also arise, very rarely, due to brain injuries, which leave one part of the brain without its normal innervation, causing invasion of neighbouring nerve fibres and a rewiring of the source of activation of a region, while the “meaning” of its activation remains the same.

Both of those types differ in many aspects from what is known as developmental synaesthesia. This is a heritable condition in which particular stimuli generate specific and consistent additional sensory percepts or associations in another sensory modality or processing stream. Easy for me to say, I know – that is such a mouthful because it has to encompass many different forms. These include seeing letters or words in colour or associating them with colours, seeing colours in response to sounds (typically words or music), tasting words, feeling tastes as tactile sensation, associating numbers or calendar units with spatial locations and many others. It is surprisingly common, with between 1 and 4% of the population estimated to have the condition.

Though originally defined as a cross-sensory phenomenon, many cases involve more conceptual inducing stimuli (“inducers”) or resultant percepts (“concurrents”). Synaesthesia may thus be better thought of as the association of additional attributes into what some psychologists call the “schema” of the inducing object. Thus, the schema of the letter “A” would incorporate not only its particular shapes and sounds, but also the fact that it is, say, olive-green. Middle C may smell of oranges, Wednesday may be located behind a person’s head and the word “shed” may taste of boiled cabbage – these kinds of associations are idiosyncratic but highly stable in individual synaesthetes.
The mechanism driving these additional percepts or associations is unknown, though most researchers agree it is likely related to functions in the cerebral cortex. This is the part of the brain where specialised areas emerge that are dedicated to processing the kinds of stimuli that often induce synaesthetic experiences or associations – such as letters, words, musical notes, numbers, calendar units. These are specialised categories, each with many different members, which are learned through experience. As a child has repeated exposures to stimuli such as letters, a particular part of the visual cortex becomes specialised for processing them, showing more and more selective responses for letters with greater experience. That region not only becomes more responsive to letters, it becomes less responsive to other stimuli. Also, learning has to sharpen the representations of each letter, so that all the various forms of the letter “A” are recognised as such, while simultaneously being distinguished from “D”, “R”, and other visually similar graphemes. In addition, the shapes for “A” have to be linked to the various sounds that it can make, in different contexts.

In contrast to the inducing stimuli, the concurrent percepts associated with the synaesthetic experience tend to be much simpler: colours, tastes, textures, spatial locations. These perceptual primitives are also typically processed by specialised circuits or areas of the cortex, but ones that mature much earlier and that develop in a manner that is not so strictly driven by experience. For example, a particular area of the visual cortex, called V4, is selectively involved in processing colour: this area is strongly activated by coloured stimuli; if it is stimulated with an electrode, patches of colour may be seen in the visual field; and, finally, damage to V4 can lead to complete colour blindness.

So, a simple model for what is happening in synaesthesia is that activation of one cortical area by an inducing stimulus (say, letters), aberrantly and consistently causes co-activation of another cortical area (say, the colour area), leading to an additional colour percept or association. Neuroimaging seems like the perfect way to test this hypothesis – if true, we should be able to see additional areas “lighting up” in functional magnetic resonance imaging (fMRI) scans when synaesthetes are exposed to stimuli that induce a synaesthetic experience.

By now, about a dozen functional neuroimaging experiments have been performed to try to define the neural correlates of synaesthetic experiences. Most of these have studied subjects with grapheme-colour or sound-colour synaesthesia and many have looked specifically for activation of V4 or other visual areas in response to the presentation of the “inducer” – either aurally presented sounds or visually presented achromatic graphemes. These have indeed provided some insights into the neural basis of synaesthesia but their findings are surprisingly variable.

Some of them have reported exactly the expected observation – extra activation of regions such as V4. However, it is not at all clear that such an effect can be taken as a ground truth, as other studies have not observed this but have seen activation or functional connectivity differences in other visual areas or in other brain regions, such as parietal cortex. Still others have observed no additional activation correlating with the synaesthetic experience at all. One early positron emission tomography (PET) study even found, in addition to some areas of extra activation in coloured-hearing synaesthetes, greater cortical deactivation in other areas in response to spoken words that induced a synaesthetic experience of colour.

What is going on in the brain of synaesthetes during a synaesthetic experience thus remains very much an open question. Phenotypic heterogeneity may explain some of the variation in these results – perhaps all of the results are “right” and mechanisms differ across synaesthetes in different studies. Even if that is the case, a simple model of excess cross-activation between highly restricted cortical areas seems too minimal to accommodate all these findings. Rather, these findings suggest that differences in connectivity may be quite extensive in the brains of synaesthetes, a hypothesis which is supported by structural neuroimaging studies. 

These studies have been performed to try and identify anatomical correlates of the condition of synaesthesia (as opposed to the fMRI experiments which are looking at the experience of synaesthesia). They aimed to test the hypothesis that cortical modularity breaks down in people with synaesthesia due to the presence of additional anatomical connections between normally segregated cortical areas. (The alternative type of model proposes altered neurochemistry, leading to disinhibition of normally existing connections).

Here, the findings are somewhat more consistent, at least on a general level. Several studies have now identified structural differences in the brains of synaesthetes compared to controls. In almost all cases, synaesthetes showed greater volumes of areas of grey or white matter or greater "fractional anisotropy" within certain white matter tracts than controls. Some of these differences are in the general region of visual areas thought to be involved in the synaesthetic experience but others are more widespread, in parietal or even frontal regions. A recent study analysed global connectivity patterns in the brains of synaesthetes, using networks derived from correlations in cortical thickness. The global network topology was significantly different between synaesthetes and controls, with synaesthetes showing increased clustering, suggesting global hyperconnectivity. The differences driving these effects were widespread and not confined to areas hypothesised to be involved in the grapheme-colour synaesthetic experience itself. Widespread functional connectivity differences have also been observed in a study using resting-state fMRI.

There is thus a strong general trend: the brains of groups of synaesthetes do show structural differences to those of groups of controls, these are concentrated in occipital and temporal regions but extend also to parietal and frontal lobes, and they almost always involve increases in the measured parameters in synaesthetes. Though the exact locations of such differences vary between studies, the fact that they all agree in the direction of the effects strongly argues that they represent a real, generalizable finding.

If only we knew what it meant. It could mean that the primary cause of synaesthesia is really a structural difference in the brain. However, the imaging parameters measured (like volume of some cluster of grey matter or fractional anisotropy of a white matter tract) are really quite crude and influenced by many variables at a cellular neuroanatomical level. What has not yet emerged is tractography evidence showing an example of connections that are clearly not present in non-synaesthetes. It is thus not obvious how the observed structural differences can explain the synaesthetic experience. It could just as well be that structural differences are secondary and arise due to a lifetime of altered activity patterns in the neural circuits involved. Or the structural differences might be entirely unrelated to the experience of synaesthesia and reflect instead some broader phenotypes associated with the condition.

With this as background, we designed a neuroimaging study aimed at probing the functional involvement in the synaesthetic experience of areas with structural differences. What we found surprised us.

We compared a group of 13 synaesthetes with a group of 11 controls (decent sample sizes for this field, but more on that below). First we looked for average structural differences between the members of these two groups. Using a method called voxel-based morphometry, we identified multiple clusters of increased volume of either grey or white matter in the synaesthetes compared to controls. We also used diffusion-weighted imaging to look at the structural parameters of nerve fibres and found multiple regions of increased fractional anisotropy in synaesthetes compared to controls. Similar to previous studies, these structural differences were concentrated in but not exclusive to the back of the brain (occipital and temporal lobes) and were all increases in synaesthetes.

So far, so good – these results generally replicate and extend previous findings. We then used fMRI to investigate how the areas showing a structural difference responded to stimuli that induce a synaesthetic experience. All the synaesthetes in the study had grapheme-colour synaesthesia – they attribute colours to letters of the alphabet. We showed them images of letters or of non-meaningful characters, as a contrast, and examined responses in nine areas of increased grey matter volume. Four of those areas showed a differential response to this contrast, in synaesthetes but not in controls (a “group by condition interaction”).

When we looked more closely at the responses in these areas we found something really surprising. Two of them showed a clear difference in response to letters, but this was driven by a very strong reduction in activity in synaesthetes. Not only was the BOLD (blood oxygen level-dependent) signal lower than in controls, it was lower than baseline in those voxels. There is good evidence that negative BOLD signals of this type reflect cortical deactivations – a suppression of neuronal activity in that region. None of the areas showed a greater response to letters in synaesthetes.

We also performed an unbiased, whole-brain analysis with the same contrast, again expecting to find regions with an increased selective response to letters in synaesthetes. We found fourteen areas showing a group by condition interaction, but none of these were driven by increased activation to letters in synaesthetes. Three of them were driven by negative BOLD responses in synaesthetes (these did not overlap the areas with grey matter volume differences).

What does this all mean?

My first thought, and I hope it is yours too, is: “possibly nothing”. After all, these are unexpected results from exploratory analyses. While they are corrected for multiple tests, they still could represent a false positive observation – a statistical blip that occurred in that experiment, with that sample, that does not represent a generalizable finding. This is a problem that dogs the fMRI literature and there is only one solution to it – replication, replication, replication! Because our study was designed as at least a conceptual replication and extension of previous findings, we did not include a separate replication sample. (It was honestly also partly because the field does not demand it). If we were designing a similar study today, I would certainly aim for a larger sample and an independent replication sample (and would hope that funding agencies would begin to apply these standards more rigorously).

Actually though, this finding is not completely novel – cortical deactivations were previously reported in response to synaesthesia-inducing stimuli in a PET study, some in the same areas we observe. Whether they have occurred in other fMRI studies is a little hard to know – experimental designs focusing on specific regions or looking specifically for positive differences may have missed these kinds of effects.

The idea that cortical deactivations might be involved in synaesthetic experiences is also neither unprecedented nor outlandish. Here’s what we say in the paper:

“One possible, though speculative, explanation for these observations relates to the fact that the synaesthetic percept or association is internally generated and often reported as being “in the mind’s eye”. A number of studies have shown that generation of an internal sensory representation induces deactivation of regions which might compete for attention or provide conflicting information. For example, visual imagery induces negative BOLD in auditory cortex, verbal memory induces deactivation across auditory and visual cortices and imagery of visual motion induces deactivation of early visual cortices (V1-3). Amedi and colleagues found a strong correlation across subjects between the deactivation of auditory cortex during visual mental imagery and their score on the vividness of visual imagery questionnaire (VVIQ). We have previously reported that synaesthetes tend to score higher on this imagery measure. This is not to suggest that the synaesthetic percepts arise from the same processes as mental imagery per se – there is evidence from functional imaging that this is not the case. But it is possible that the vividness of a mental image and of a synaesthetic percept both rely on deactivation of other areas. 

Such a conclusion is supported by findings from a transcranial direct current stimulation (tDCS) study.
[This technique basically hooks up a 9-volt battery to electrodes on your scalp, and applies small zaps of current in particular patterns. It can be applied to affect particular regions and to either activate them or inhibit them. Activating motor cortex can cause muscle movements while activating visual cortex can cause perception of winking lights or “phosphenes” in the visual field].

Terhune and colleagues found that synaesthetes showed enhanced cortical excitability of primary visual cortex, with a 3-fold lower phosphene detection threshold in response to activation by tCDS. [This finding is consistent with a previous study from our own group using electroencephalography, which found that the amplitude of early visual evoked potentials was larger in synaesthetes compared to controls, even in response to very simple visual stimuli that did not induce a synaesthetic experience].

They tested whether this hyperexcitability of primary cortex could be either a contributing source to the generation of the synaesthetic percept, or, alternatively, a competing signal, which would interfere with the conscious perception of the synaesthetic percept. They show strong evidence that the latter is the case – stimulation or inhibition of primary visual cortical activity diminished or enhanced, respectively, the synaesthetic experience, based on both self-reports and behavioural interference measures. It thus seems plausible that the cortical deactivations we observe in response to stimuli that induce the synaesthetic experience could be an important part of that response, possibly involved in reducing the signals of competing percepts and allowing the internally generated synaesthetic percept to reach conscious awareness.”

Future studies will hopefully tell whether these kinds of cortical deactivations really are an important component of the synaesthetic experience. For now, our findings add to a quite varied set of neuroimaging findings, which have yet to definitively nail down the neural correlates of the synaesthetic experience. Perhaps expecting a single mechanism is a mistake – if the condition is really heterogeneous we may need some other means (like genetics perhaps) to segregate subjects and elucidate the neural underpinnings of this fascinating condition.

Monday, September 2, 2013

Why optogenetics deserves the hype

Optogenetics has come in for some stick lately, with a number of people criticising the hype that this technique generates in some quarters. That’s fair enough, I suppose – there have no doubt been some claims made about what can be accomplished with this technique that are, at the very least, premature. I’m all for bashing hype (see The Trouble with Epigenetics 1 and 2, for example), but criticising the technique for what it’s not good for seems to be missing the point to me.

To me, optogenetics will revolutionise neuroscience. It is the tool that will finally let us meaningfully integrate the cellular with the systems level. Not by itself, of course – we’ll still need all the electrophysiology and pharmacology and neuroimaging and lesion studies and model organisms and whatever you’re having yourself. And not without some teething problems and over-interpretation of early findings, which will no doubt earn more tongue-lashings from the hype-police. But it will let us ask questions we have not been able to ask before – the right questions, at the level of cell types, the fundamental functional units of the nervous system.

Before I go on, a brief primer on how optogenetics works: this technique takes advantage of a number of proteins found in various species of algae that respond to light of certain wavelengths by opening a channel in their cell membrane to allow electrochemical ions (like sodium or chloride) to flow in or out of the cell. Controlling the flow of such ions along their fibres is also how neurons conduct electricity. If you take the gene that encodes the light-sensitive channel from algae and force neurons to express it, then they will become responsive to light – if you shine a light on them they will “fire” an electrical signal, or “action potential”. If you turn the light off, they will stop firing action potentials. And if you use a different channel protein, you can silence the neurons and stop them firing action potentials. This gives very tight, reversible control over the activity patterns of the neurons expressing these channel proteins (called channelrhodopsins).

The trick, and the power of the technique, comes from the specificity with which you can direct that expression. This is based on the fact that different types of cells express different sets of genes. All genes have two main parts – one part is basically the recipe or code for a particular protein. The other part, which is encoded on a neighbouring piece of DNA, is the regulatory region – the instructions for when and where to make that protein and how much to make. Those two regions can be separated. You can cut out the DNA that makes up just the regulatory piece of one gene and hook it up to the protein-coding region for any other gene you like (in this case, a channelrhodopsin protein). Now you can take that fusion gene and introduce it to cells or transgenically introduce it to animals, like worms or flies or mice. Such animals will now express channelrhodopsin only in the cell types directed by the regulatory piece of DNA you chose. A variety of other molecular methods can also be used to achieve this goal, including resources based on binary systems like the Cre-LoxP recombinase system. (Fibre optics can then be used to target light to those cells in particular brain regions).

So how many different cell types are we talking about? Going by the kinds of animations common in science fiction movies, many people apparently think of the inside of the brain as a network of effectively identical cells, randomly placed in a sponge-like layout, connecting simply to their nearest neighbours. Nothing could be further from the truth. We have known since the time of Ramon y Cajal and Golgi that there are many distinct types of neurons, which are distributed in a highly organised fashion in different brain regions and interconnected with exquisite specificity. And when I say many, I mean many hundreds, possibly thousands of types.

The retina alone has over 60 distinct, recognised neuronal cell types and more subtypes are being defined all the time. Those 60 cell types are arranged in four or five distinct layers, with multiple subtypes in each layer. There are at least a dozen parallel pathways across these several layers, processing various aspects of the visual stimulus – colour, form, direction, motion and many others. If you want to understand how the retina works – to reverse engineer it – you need to know what the functions of these cell types are within the context of the circuit in which they are embedded.

The importance of cell types as functional classes is blindingly obvious for the retina, but the same principle applies to any area of the brain. Subsets of cells in any area not only have discrete jobs to do within that area, making unique contributions to the computations carried out there, they also often connect in distinct, cell-type-specific, parallel circuits with other brain areas.

In the cerebral cortex, different excitatory cell types are arranged into six obvious layers, but these often have several sublayers. And within each layer, there are multiple subtypes of excitatory neuron, intermingled. In layer 5, for example, some neurons project across the corpus callosum to the other hemisphere, some within the cortex on their own side and others to subcortical targets. Each of these types contains multiple subclasses carrying information to distinct targets. That cellular complexity is multiplied by the number of cortical areas – subcortically-projecting layer 5 neurons in motor cortex are molecularly distinct from those in visual cortex, for example.

And we haven’t even started on the interneurons. These are smaller, more locally projecting cells, which are inhibitory – they put the brakes on excitation in neural circuits. They not only prevent runaway excitation, but also, crucially, control many aspects of information processing, such as filtering, gain control and temporal and spatial integration. In addition, they orchestrate the synchronous firing of ensembles of excitatory neurons, which in turn is a central mechanism in mediating communication between brain areas. Just in the hippocampus, there are twenty-some subtypes of interneurons already known, and, again, more are being defined all the time. Each of these subtypes is distributed in a particular manner, expresses different kinds of ion channels and neurotransmitter and neuromodulator receptors and makes specific kinds of synapses on specific subcellular locations of specific target cells.

We cannot ignore this cellular complexity, but, until recently, we have had few options for really embracing it. As long ago as 1979, the central importance of cell types was recognised. Francis Crick had seen the power of molecular genetic techniques in other areas of biology and knew that, with the right tools in hand, it could be harnessed to help unlock the mysteries of the brain. His article in Scientific American’s, “Thinking about the Brain” explicitly described three needed methods for neuroscience to make real progress: first, a method by which “all the connections to a single neuron could be stained”; second, a method by which “all neurons of just one type could be inactivated, leaving the others more or less unaltered”; and, third, a means to differentially stain each cortical area, “so that we could see exactly how many there are, how big each one is and exactly how it is connected to other areas.”

While connectomics on various scales is addressing the first and third of these, optogenetics provides the means to accomplish the second. Indeed, it surpasses the requirement Crick had in mind, by allowing not just inactivation but also activation, with exquisite temporal control and rapid reversibility. (As it happens, optogenetics is also a fantastic method for mapping functional connections between cell types).

Using optogenetics, we can move beyond the crude methods of lesion studies or stimulation with electrodes inserted into a particular brain region. These methods are hopelessly confounded by the intermingling of cell types within the targeted regions. In any given area, it is typical to find multiple cell types that directly antagonise each other – lesioning them all or stimulating them all may not reveal the complex functions and computations carried out by the region in question. Optogenetics simply provides a much more precise, selective and controllable method to perform these kinds of investigations.

One example is provided by the circuitry controlling appetite. The arcuate nucleus in the hypothalamus is a crucial hub in this signaling, integrating signals from the periphery, such as leptin and insulin levels, and passing these signals on to further hypothalamic regions which mediate feeding behaviours. Lesioning the arcuate nucleus has little effect on feeding behaviour, however. The reason for that was discovered once the leptin receptor and other players in this system were cloned and molecular genetic characterisations revealed two major cell types intermingled in the arcuate nucleus. These directly antagonise one another and communicate opposite signals to downstream areas – it is the balance between their activities which controls behaviour. Several recent optogenetics studies have now greatly increased our understanding of this system, mapping connectivity to specific cell types in downstream target regions, revealing the hierarchy of their functional relationships and directly demonstrating short- and longer-term effects on behaviour of activity of these different neuronal classes.

These experiments are not just elegant and precise, they are powerful and incisive – they are the right experiments to do to understand this system because they interrogate the system at the right level: the distinct cell types that make up the fundamental computational units.

Another reason I am so excited by optogenetics is it provides one means to integrate analyses at very different levels, uniting what have been disparate areas of neuroscience. The characteristics of individual neurons or specific synaptic connections are traditionally analysed by molecular and cellular neuroscience and electrophysiology. The roles of specific neurotransmitters or receptors are probed with pharmacology. The functions and interactions of brain areas are studied using field recordings, electroencephalography, neuroimaging, lesions and other systems neuroscience methods. These approaches have traditionally been carried out by different people with different skills and different mindsets.

While we may have learned a lot of details at each level, integrating knowledge across those levels has remained a huge challenge. As a result, we have had little real understanding of how the functions of any brain area emerge from the interactions of its component cells.

Optogenetics provides a method to connect those levels. By inhibiting or activating entire classes of neurons within a region and analysing the effects on activity in other cells or regions or the effects on behaviour of the animal, on a moment-to-moment basis, we can discern the functions which these cells and circuits have evolved to perform.

And that’s the key, really – evolution has built the mammalian brain by elaborating on basic plans already present in our distant ancestors. In simpler organisms it is possible to identify not just types of cells, but individual neurons – in nematodes, the 302 neurons have all been named. In insects, you can see the equivalent individual neurons repeated in each segment of the ventral nerve cord. Those nervous systems function based on the actions of individual neurons and their interconnections. Mammalian brains function more at the level of ensembles of neurons, but the basic logic is similar – evolution has built these brains by expanding the numbers of cells of ancestral types, so that what was once a single neuron is now a population of neurons of the same “type”. Evolution has also increased the diversity of subtypes, which are deployed and combined in myriad ways to generate the incredibly complex circuitry we seek to understand. 

That is the reason I argue that cell types are the fundamental units of the nervous system and why optogenetics is such a powerful method to help move neuroscience from crude and fragmented approaches to a united field capable of explaining how the operations of the mind emerge from the workings of the brain.

Let me add a few notes:

First of all, I don’t have a dog in this fight. I have no stake in any optogenetic technologies and don’t currently use the method, though I certainly hope to in the future. I’m simply really excited by its potential. I don’t get giddy over new techniques very often, but when I saw Karl Deisseroth present his team’s work at the first Wiring the Brain meeting in 2009, I was blown away by its potential – along with the rest of the audience of hard-to-impress neuroscientists.

Second, optogenetics alone is not the answer to all things – it is a method that is suitable for asking specific kinds of questions. There are, in addition, numerous conceptually similar molecular genetic techniques now being used or developed, which greatly expand our arsenal of tools for monitoring and manipulating patterns of neuronal activity.

Third, let’s consider a few of the common and recent critiques of the method:

1.     The drivers we are using do not target real cell types, because they depend on the expression pattern of single genes, while real cell types are defined in a combinatorial fashion by the expression of multiple genes. That is absolutely true, but intersectional strategies (which drive expression only where two genes intersect) are greatly increasing the specificity possible. Also, combining transgenic drivers with viral systems that can be delivered to specific brain regions can address many of these issues.

2.     We don’t know what stimulation protocols to use. Just blasting some neurons so they fire like crazy does not recapitulate the real patterns of firing seen in vivo. Also true, though that criticism applies to traditional electrical stimulation as well. But molecular genetic tools designed to monitor and measure these patterns have also been developed and such patterns can be retransmitted through the sensitive, rapid and reversible optogenetic drivers.

3.     It’s not good for studying neuromodulation – the slow signaling which is so important for changes in the functions of neural circuits over longer timeframes. This is just wrong. You just need to target the neuromodulatory neurons – the ones that release dopamine or serotonin in response to action potentials that they fire. Many of the most exciting early papers using optogenetics have taken this approach. In addition, new techniques, like DREADD, have been developed to directly activate G-protein-coupled receptors in a way that closely mimics neuromodulatory effects.

4.     It can’t replace lesion studies. Yes, it can. Or at least it can provide a crucial complement. Lesion studies are great for studying the effects of lesions to specific areas (of obvious clinical importance) but limited for inferring how the functions of those areas are mediated, for the reasons outlined above.

5.     We can’t use it for therapies because we don’t know which brain regions to target. Well, first off, deep brain stimulation is currently in use for conditions like obsessive-compulsive disorder and Parkinson’s disease and is showing great promise for depression. Optogenetic approaches may provide a more sophisticated method to control neural activity, which is directed to specific cell types within the target region. This is likely a long way in the future and would involve the complex issue of transfecting human brain cells with viruses, but it is clearly a theoretical possibility and an interesting avenue to explore. Secondly, optogenetics is primarily a research tool – one that we hope will lead us to a greater understanding of brain circuit function and dysfunction, which, in turn, will allow us to develop new therapeutic approaches. When people like Karl Deisseroth talk about its relevance to psychiatric disease, this is what they mean: “Despite the enormous efforts of clinicians and researchers, our limited insight into psychiatric disease (the worldwide-leading cause of years of life lost to death or disability) hinders the search for cures and contributes to stigmatization. Clearly, we need new answers in psychiatry.” As quoted and misrepresented here.

Finally, to end on a positive note, here are a few of my personal favourites from the recent literature where optogenetics approaches have generated real and novel insights into the organisation and function of specific brain circuits: