A lesson from William Harvey in the XVII century on the value of model organisms

Screen Shot 2014-09-14 at 17.25.26It is well known that history repeats itself but, as we have limited memory and a tendency to think about ourselves and our times, we forget the lessons from the last time it came around. Let me tell you a story. Like many of you I associate William Harvey with the wondrous discovery of the circulation of the blood and the identification of the heart as the pump that keeps this movement going. I also was aware that he performed the first proper or recorded measurement in biology as the amount of blood going around the body in a given period of time. This was to show that for the number to be true the blood could not be supplied by some infinitely powerful source in the liver but most likely, circulated. As a developmental biologist I was also aware of his late book on the generation of animals (Exercitationes de Generatione Animalium, 1651) in which he describes the development of many organisms, with a particular emphasis on chickens and deers, and speculates on their embryological origin. In fact, this book was a summary of research conducted over many years which he would not have published had it not been for the intervention of George Ent, a friend who was aware of this work and encouraged, almost obliged him, to let it out . In many ways and despite its frontispiece (Omnia ex ovo), the book is a minor work compared to “de motu cordis” and, as has been acknowledged by historians, has more questions than proper answers, but does represent a major contribution to the development of embryology. These facts I knew, but a recent reading of the excellent book “Circulation’ by Thomas Wright, on the way Harvey worked out his theory about the heart, alerted me to facts I did not know, which made me realize HOW he worked out his remarkable conclusions. The process that led to “de motu cordis” made me see some features of his research which are interesting in the light of modern science. 

Harvey was a doctor who rose very quickly to a position of prominence in the London establishment. He had attended Cauis College in Cambridge (as my colleague David Summer never ceases to remind me!) and then, impelled by the flow of the time, went to Italy to follow his interests in Medicine and Anatomy; a  graduate study of sorts. It was there, in Padua, where where he became acquainted with the issues of the time in particular the details of the behemoth that was Galenic medicine.  Amidst his teachers there was Fabricio de Aquapendente, a doctor with an interest in anatomy and who was a pioneer comparative embryologist and who became a significant influence in Harvey’s studies. The organization and function of blood was a central issue of study at the time where the centuries old views of Galen prevailed. Essentially, blood mainly manufactured in the liver, ebbed and flowed through veins and arteries to end in the tissues within an open ended system. The heart was the source of heat and of the spirit, and acted as a sort of mixing blender; though an important organ it was not so important as the liver. There were alternative, speculative ideas around about the heart and Harvey took note of them. After his studies, he went back to England and quickly rose through the ranks in London medical society to become associated with the court, teaching anatomy and, eventually, becoming the Doctor of the King, most notably of Charles I. But all this is secondary to this story.  In the back of his mind, though, was the question of the workings and function of the heart. In a series of remarkable experiments conducted over a period of more than 10 years (a core of 1615-1625 can be identified by experts) in a laboratory set in his house, he developed and reasoned the theory that the heart was a plumbed pump that moves blood around the body. As a consequence of this study he assigned the correct function of veins and arteries and identified the direction of the circuit. Now, and here is my point. The knowledge came from a comparative study and without such a study he could not have reached the conclusions or, better, the detail supporting the conclusions. By comparative I mean, comparing different organism on the correct assumption that there is a conserved plan. You should read Wright’s book. It is a gem.

The studies began with corpses that he procured because of his association with hospitals but then, if you want to think of a pump, you need to see it at work. He did that, as it was customary at the time, with vivisected animals, principally dogs. A bit sensitive these days and as Wright points out, no less then but, on the other hand, necessary. One of the issues at stake was the function of the systole and diastole, the periodic movements of the heart which result in its physiological outputs. There was a debate as to which was the active phase and was a problem as all Harvey had to solve it was direct observation. The movements are too fast in mammals for him to discern the relationships between the actions and the consequences, with regard to the blood, and he puzzled and surely wrestled with his intuition and the facts. Notwithstanding this, as the animal died, the movements slowed down and he could get glimpses of how the system worked. But he needed to prove it in the living organism. Here is where it gets remarkable, at least in my eyes. In a series of studies, he looked at the circulation of the blood and the activity of the heart in a range of organisms from slugs to dogs, but paying special attention to cold blooded animals where the movement was slowed. In a particularly interesting study he watched the relationship between the pumping of the heart and the movement in some fish he got from the Thames. You cannot miss it in the glory of the zebra fish, as my colleague C Schroeter who worked with this organism remarked: it is a wonderful thing to SEE the blood leaving the heart through the aorta to the beat of the heart and this is published even if Harvey had seen this 400 years ago. These observations buttressed his views and made a seminal point for the circulation of the blood. Let me highlight the point: it was the model organisms that established in Harvey’s mind the universal principle that changed medicine and our notions of the heart forever. Of course, as you might have expected, when he put his views to the then public peer review, amidst many of the questions that came up, that of the actual value of the functioning of the heart was one of them but, another one was the value of the events in frogs and fish to humans. We would say that it was the XVII century but if you think about this you will find a parallel in today where the drive towards human biology often forgets and renegates of how much we have learnt from model organisms. 

Screen Shot 2014-09-14 at 17.08.21One very important point is that Harvey used the different organisms to answer an important question and this can be easily lost in the fog of today’s emphasis on publication and superficial ‘novelty’.  The major contributions of model organisms to current biology have been on important, general questions. The principles of genetics were worked out in plants and animals but this was not the place to look for the molecular nature of the gene. This required going to phages and bacteria on the assumption, which turned out to be correct beyond expectation, that it would be universal. This was the same as with Harvey (a fish heart is a heart as much as a human heart – much to mull over on such statement in the XVII century), and also guided us to unravel the genes that drive development -using flies and worms- the principles of early development -with frogs and chickens. In all cases, model organisms, as we have come to call them, have been instrumental. The current focus on mammalian and, in particular, human biology and the attempts to sidestep model organisms should take stock of the fact that model organisms have been a staple of medical and biological research since the times of Aristotle and that great discoveries, like that of Harvey, could not have been made without them. 

I want to end up with another, perhaps more subtle, analogy with the events 400 years ago. Harvey faced a problem, a serious one. The whole of the medical profession at the time was built around Galenic medicine. The open circulation model created an array of easy to implement cures for a variety of diseases through bleeding that were performed by the physicians at a costly price. If Harvey was right the whole system needed to change and many of his colleagues were, as it indeed happened, out of business. Sometimes the lessons from model organisms are hard to take and many people will resist them. 

There is an ongoing debate about the importance of supporting research in model organisms and as someone who has spent many years working with Drosophila I am in favour of this. However, it is important that we do not lose sight that the relevance of a model organism is related to the significance of the question that one asks in it. The technological advances and the cottage industry that has emerged around them leads some times to derivative science which has no other purpose of the publication. Let is use model systems but, like Harvey, to answer a good question; only then they will be vindicated and we shall put them in their rightful place.

A few references

Aird, WC. (2011) Discovery of the cardiovascular system: from Galen to William Harvey. J Thromb Haemost 2011; 9 (Suppl.1): 118–129.

Donaldson, IML. (2009) William Harvey’s other book: Exercitaciones de generatione animalism. J R Coll Physicians Edinb. 39:187–188.

Kilgour, F. (1961) William Harvey and his contributions. Circulation 23, 286-296. doi: 10.1161/01.CIR.23.2.286

Wright, T. Circulation: William Harvey’s revolutionary idea.

There is also an excellent movie about Harvey’s experiments: https://archive.org/details/WilliamHarveycirculationoftheblood4-wellcome

NB The image of the frog on the mouse is taken from http://letsbefriends.blogspot.co.uk/

A new forum for Physics and Biology in Cambridge

The Theory of Living Matter is a new discussion group in Cambridge led by young physicists from the Theory of Condensed Matter (TCM) group in the Cavendish (Cambridge). The idea behind the group (www.tcm.phy.cam.ac.uk/tlm/) is to promote interactions between theorists and experimentalists in the realm of the biological questions and serve as a forum and a local hub for this topic. There have been two meetings to date with a fair amount of success.

This is a very good time for physicists to get into Biology and for biologists to deal with physicists. The main reason for this is that there is data and that therefore theory need not be some abstraction that describes a reality which does not exist; this has happened several times before and a good example is the surge of mathematical biology in the 60s and 70s which, deservedly, did not go very far because there was little to model or theorize about. Nowadays it is different, There is a huge amount of information or data (depending on who you talk to) waiting for an explanation, for a framework, for a model. Physicist (and mathematicians and engineers in the same group) are talking to biologists but for these two cultures to partner successfully there have to be some rules and here I would just like to provide some thoughts from my own experience over the last ten years.

For biologists, the most important point might surprise us (I am a biologist) and is encapsulated in two statements that an eminent biophysicist made to me many years ago and changed my view of Biology. They are obvious. We need to learn to measure and also appreciate the differences between averages and distributions. The first one is very important and might sound odd: physicists telling us that we need to measure? Physicists suggesting that we do not know how to do an experiment? Don’t we spend our lives doing experiments? Well, yes. But I am afraid that in the days of kits and, sequencing by post and high throughput-anything, our ability to make accurate measurements that give information has dwindled. I would even argue that our ability to even have our experiments driven by hypothesis is a thing of the past. Well, yes, this happens more in some disciplines than others but it is a trend. There are two exceptions. One is cell biology where a large influx of physicists over the years has created a good culture of measurement, hypothesis and quantitative science. The other one is, of course, evolutionary biology which today lives a Renaissance because of the abundance of data to check theories and test models. But in genetics and molecular biology things have drifted and for the most part we design experiments not with the idea of obtaining a measurement but with that of obtaining a result. This, of course does not apply to everybody but……….It is interesting that in many places computational biology is understood as advanced bioinformatics. So, it is indeed important that when we (biologists) design experiments we have a question in mind and ensure that we aim to get a measurement, a number.

The second point, the difference between averages and distributions, is trivial for those in the physical sciences and yet, it is totally unappreciated by the biologists; though I shall admit that this is slowly changing. A great deal of Biology is based on average values. A phenotype is an average value and this is what we use as reference in many different situations. Where before we had just an image or, as they say, a ‘representative image’, nowadays we often have some values, charts, with error bars which is, still, an average. This might work in some instances but we should think about whether it is the appropriate measure of what we need or not. Distributions are far too often neglected ignoring that it is here that lies the information. There are variables which under different circumstances have the same mean which results from different distributions; it is the distribution that matters, The trivial case here is cell division: a survey of a population in culture would show some cells dividing and some cells not dividing which would suggest that, on average, a cell divides 0.5 times. This makes no sense: the distribution and not the mean is the information here.

The importance of these two pieces of advice or realizations is that as we go beyond hunting genes and linking them to phenotypes, we are starting to see that cells, really the product of gene interactions, produce numbers and we need to understand those numbers. As any physicist knows, seeing the distribution associated with a variable is a way to get into the mechanism (in the sense a physicist uses this word: a causal explanation for an observation rather than Figure 8).

And while we are talking about physicists I also have something to say to them as to how to deal with biologists. A renown physicist doing biology starts many of his talks stating that he is a theorist and that without data he is disabled. As if experimentalists could live without data! As if we, biologists, just would like to potter around and this were the aim of our toilings!  Experimentalists are also theorists and this is something that any physicist, particularly theoretical physicist needs to appreciate when interacting with Biology. When an experimentalist probes into Nature, is not just pottering around, we are testing a hypothesis and sometimes a theory. Theoreticians running into Biology should bear this in mind. A physicist will be better prepared than a biologist to understand a measurement, maybe even to design an experiment, but there will be a need to understand that biological systems are not physical systems (‘From molecular to modular cell biology.’
Hartwell LH, Hopfield JJ, Leibler S, Murray AW. Nature. 1999 ). The differences will drive a physicist mad but if understood properly will bring some joy. And by the way, if you are a physicist getting into Biology, get as close to experiments as possible and even dip your fingers and your mind into an experiments. R. Feynman and F. Crick did it. Feynman worked for a while (well, a few weeks) in the lab of Delbruck in Caltech. At the time the hot topic was the genetic code and, as it happens, Feynman isolated some of the first intragenic suppressors. But Biology did not grab Feynman: too much variability, too early for predictions and calculations. The one who got hooked was F. Crick and you can see how and why in his book “What a Mad Pursuit’ where you can see his sharp mind in action and find much that is good about the role that physicists should play in Biology.

As a local, I am very pleased about the development of the Theory of Living Matter forum. Anything that is done to bring the ideas and methods of the physical sciences into Biology is a good thing but, more importantly, it is something much needed at the moment.

Grasping at straws

“let us hope that it is not true but, if it is true, let us make sure that it is not widely known”
Anonymous comments to the idea of Evolution.

A pdf of this blog can be downloaded here.

Nature has dedicated two News and Views to a recent piece of work on Wingless (1), thus emphasizing its importance. Both comments focus more on the notion of Wingless as a morphogen than on other aspects of the work. The reason might lie in the fact that much of the notion about Wnt signalling in mammals is derived from the analysis and interpretations of work in Drosophila. The manuscript of Alexandre, Baena and Vincent (1) suggests that in Drosophila the long range action of Wingless is not functionally significant, thus inviting a reassesment of our understanding of the function of Wnt proteins. Surprisingly, both comments read like health warnings. Here I would like to comment on the one from Gary Struhl (2) who appears to cast some doubt on the ability of the experiments in the manuscript to debunk the belief that Wingless acts as a long range morphogen in Drosophila.

Gary Struhl has spent a life time extolling the virtues of Morphogens in pattern formation and devising experiments to prove their existence in Drosophila. His comment raises doubts over the findings of the paper but has a number of factual inaccuracies, misleading statements and missing references which need pointing out.

The opening statement of the News and Views makes clear how uncomfortable the author is with the work of Alexandre, Baena and Vincent: “There is compelling evidence that Wg can, and normally does, act over many cell diameters to control gene expression and growth of the Drosophila wing. So the remarkable discovery that a membrane-tethered form of Wg can substitute for the normal protein poses the question: must morphogens move to organize development? When considering this challenge to how we think of morphogens, the devil is in the details”. A strong statement to which a learnt reader can only say: really? where is that compelling evidence? A give away to its source is that the three references in support of the notion are two papers by Struhl himself (3, 4), and one by Cohen (5), another advocate of the Wingless = Morphogen notion. Self interest? Perhaps, as far as some of us remember, the best evidence was, as it appears to be now, the repetition of the mantra “Wingless acts long range and therefore it is a morphogen” which is in the title of many papers.

I agree with Struhl on one point: that the devil is in the detail. But perhaps not where he wants us to look into but rather in the work of the 90s. So, let us look at some details (with apologies to all who have heard the story before but Struhl’s views suggest that it is worth repeating and, in any case, there are a few new issues that I had not wanted to review earlier). I shall not discuss the work of Neumann and Cohen as it contains little to even discuss (in fact this manuscript is apt for that accolade of the physicist W. Pauli of ‘not being even wrong’) and, what is worth discussing, has been addressed in the literature (6).

The details the devil forgot

Let us start with what is missing.

It is far too often forgotten that there has been evidence in the direction of the work of Alexandre et al for over 20 years but that Struhl, Cohen and other prominent researchers, decided to ignore it throughout the 90s. The early arguments in favour of the Wingless = Morphogen notion were derived from work on the wing disc of Drosophila. Here the “idea” was that during larval development Notch signalling sets up a stripe of Wingless expression along the dorsoventral boundary of the developing wing disc which was thought to act as the Organizer/Morphogen/whatever-you-wanted-to-call-it, to rule the growth and patterning of the wing. This is, essentially, the view subscribed by Struhl. The number of papers and reviews supporting it during the 90s and 00s is very large to the point that the notion made it into textbooks and the psyche of developmental biology. In fact it has become the view in vertebrates where there is very little evidence to support it at the moment. But, as I have said before, there was phlogiston in the wing (http://amapress.gen.cam.ac.uk/?p=1191) and, particularly in the work of Struhl and others, the devil never looked at the details of the experiments and forgot others which challenged it.

In summary, there are two sets of experiments that were (and I may add are) consistently ignored that argued against their case. The first one, that removal of the stripe of Wingless did not affect the growth and patterning of the wing (7) (this has since been confirmed by the work of JP Vincent and his colleagues (8) which to their credit never fell for the Morphogen notion). This work is, once again, ignored in the commentary and should have been addressed as it is a sound observation that supports the findings of the paper (I should add that, for some reason, it is also not mentioned in 1). The second set of experiments involved attempts to rescue the loss of wing of Notch mutants with overexpression of Wingless or Armadillo –as the mantra says should happen. It never worked (6, 9). It has always been puzzling that people who talked about Wingless as a Morphogen never deigned to even discuss these results. Late in the game Giraldez and Cohen tried hard to exorcise them but could not (10); even Struhl himself had to accept some of them (11).

Warning: One experiment that was used by some people to claim an involvement of Wingless in the growth of the wing is the emergence of an ectopic wing from the notum (apologies for the technicality) when Wingless is overexpressed in a particular region of the wing disc. The interpretation of the experiment is a misconception and a misunderstanding of the development of the disc. It would take too long to discuss this and I refer the interested reader to places where an explanation has been elaborated at length (6, 9, 12). In essence, the pattern of expression hits a sweet spot for the initiation of wing development and what one is doing is using Wingless to start (not to organize) the development of another wing.

Another detail against the Wingless=Morphogen notion concerns the effects that Wingless has on proliferation, or growth if you will. This is a subtle issue but, attempts to look for an effect of Wingless signalling on proliferation in the wing have been unsuccessful (NB in the sense of whether loss or gain of Wingless or ß-catenin alone affects proliferation e.g 13). However, loss of function of the receptor, Arrow (LRP5/6), does affect viability (10) and there are some truly intriguing observations from mosaics in experiments of the Vincent lab (14 and see also 8) that deserve some close attention. They suggest that the interactions of Wingless signalling with other pathways might be more important than what Wingless can do on its own (see e.g 15). This is most clearly seen in its interactions with Vestigial (9 and also discussed very nicely by Struhl in 4). But this is a different matter and does not detract from one fact: there is little evidence that, on its own, Wingless affects growth, and certainly none that it does so as a long range signalling molecule.

In summary: there is abundant evidence that the stripe of Wingless expression that emerges at the same time in the first day of the third larval instar does not act as a long range instructive source of Wingless for the development of the wing.

The devil in the roots of the mantra: the “direct and long range action of Wingless”

Here I would like to address a number of issues on the results of the work from Struhl’s lab which is the cornerstone of his views of Wingless as a Morphogen (3). This might be tedious for some readers so I shall summarize; for those interested in details (and there are some juicy ones) I suggest you go the Appendix or/and download a full length version of this post at the top.

In summary, a close look at the results in this work (3 published in Cell) reveals

1. Low quality data

2. Uncritical analysis of the results which, for the most part, are made up of a series of selected correlations

3. No details of how the crucial experiments were performed (no genotypes, no details of developmental timings, no landmarks that allow one to evaluate the experiments)

4. No epistasis which would allow a test of whether Wingless is or is not a Morphogen

5. Most worryingly, an experiment in Figure 1 which is either impossible or, at best, puzzling. Having consulted with colleagues familiar with the system none of them understands what panels E and F are and, if they are what is said, how are the results obtained (for details see Appendix).

Unfortunately, details are not a strength in the papers quoted by Struhl, particularly about timings and patterns of expression of Wingless. This perhaps explains the lack of understanding of the work of Alexandre et al. as Struhl and colleagues have rarely strayed from the third instar discs. As clearly shown and discussed by Alexandre et al (and see also references 6, 7, 9, 12, 16. 17 and timeline) the DV stripe of Wingless emerges rather late, certainly not before the beginning of the third larval instar, by the time the wing has almost finished the bulk of its growth. Before this, Wingless goes through a succession of patterns but not in the manner relayed by Struhl : “On the first day, Wg, is broadly expressed, but its expression fades progressively in the more dorsally and ventrally positioned cells, generating Wg gradients”. This is an oversimplification of a sequence of events that take place over four days and involve not the simple change minimalistically depicted in the News and Views but a series of patterns of patterns of expression under different controls (see Figure below and 12, 16, 17). A failure to grasp the details of this sequence of events and take them into account in the design and interpretation of experiments can be fatal. And in the case of reference 3, it is (see Appendix)

Grasping at straws-1 copy

Another feature of the News and Views is the clear mistake in the accompanying figure. I am sure that Struhl has nothing to do with this but notice that the Nrt-Wingless (membrane tethered) wing of the figure shows a reduction of about 35-40% of the normal size, whereas the same wing in the manuscript (the same wing! The same experiment!) shows a much smaller reduction of about 10%. This means that the effect is exaggerated in the News and Views in a manner that suggests, falsely, that the Nrt-Wingless wings are not normal –which is not the conclusion of Alexandre et al.  Given the interest of the News and Views to question the results of Alexandre et al. if Struhl has not had access to the flies, I would suggest that this is a manipulation of the original data to favour the point of the commentary. The legend of this figure ends up with a statement: it remains unclear how the long-distance Wg signalling thought to be required for wing development is exerted in these flies. Well, leaving aside the manipulation of the figure, perhaps the answer lies in that THERE IS NO LONG RANGE FUNCTION OF WINGLESS.

Grasping at straws-2

Figure shows wings from the wild type (outer outline) and Nrt-Wingless flies as reported in the manuscript of Alexandre et al (red dotted rim) and as represented in the News and Views by Struhl (blue dotter inner rim). Notice that the inner perimeter is said to represent the red dotted one.

In summary: the dangers of being seduced by the ideas

The problem with looking at details is that, in the case of Wingless=Morphogen, the more one digs into the experimental foundation of the idea, the harder it is to understand not just the claims of the News and Views but how the developmental biology community was seduced by an idea for which there was so little evidence. Struhl appeals to the need to look at the small print in the experiments of Alexandre et al. and in doing so is grasping at straws. Is he claiming that homeopathic quantities of Wingless liberated from the membrane tether are mediating the morphogen function? I suggest that he looks into his experiments and sees how much of the evidence he uses can be sustained today. His arguments read like the comments of a polite reviewer 3 whose experiments have not yet been done. More to the point they echo that victorian lady commenting on Darwinism: let us hope that it is not true but, if it is true, let us make sure that it is not widely known.


1. Alexandre, C., Baena, LA. Vincent JP. (2014) Patterning and growth control by membrane-tethered Wingless. Nature 505, 180-185.

2. Struhl, G. (2014) Long range thinking. Nature 505, 162-163.

3. Zecca, M., Basler, K. & Struhl, G. Cell 87, 833–844 (1996). Direct and long-range action of a wingless morphogen gradient.

4. Zecca, M. & Struhl, G. (2007) Development 134, 3001-3010. Control of Drosophila wing growth by the vestigial quadrant enhancer.

5. Neumann CJ, Cohen SM. Long-range action of Wingless organizes the dorsal-ventral axis of the Drosophila wing. Development. 1997 Feb;124(4):871-80.

6. Klein, T. Martinez Arias, A. (1998). Different spatial and temporal interactions between Notch, wingless and vestigial specify proximal and distal pattern elements of the wing in Drosophila . Dev. Biol. 194, 196-212.

7. Couso, J.P., Bishop, S. Martinez Arias, A. (1994). The wingless signalling pathway and the patterning of the wing margin. Development. 120, 621-636.

8. Piddini E, Vincent JP. (2009) Interpretation of the wingless gradient requires signaling- induced self-inhibition. Cell 136, 296-307.

9. Klein, T. Martinez Arias, A. (1999). The Vestigial gene product provides a molecular context for the interpretation of signals during the development of the wing in Drosophila. Development 126, 913-925

10. Giraldez AJ, Cohen SM. (2003) Wingless and Notch signaling provide cell survival cues and control cell proliferation during wing development. Development 130, :6533-6543.

11. Zecca M, Struhl G. (2007) Control of Drosophila wing growth by the vestigial quadrant enhancer. Development 134, 3011-3020.

12. Martinez Arias, A. and Stewart, A. (2003) In molecular principles of development. OUP. Look up at  Fig 12.21 and the associated section pp 382-389.

13. Johnston, L. Sanders, AL. (2003) Wingless promotes survival and constrains growth during Drosophila wing development. Nature Cell Biol. 5, 827-833.

14. Baena-Lopez LA, Franch-Marro X, Vincent JP. (2009) Wingless promotes proliferative growth in a gradient-independent manner. Sci Signal. 2009 Oct 6;2(91):ra60. doi: 10.1126/scisignal.2000360.

15. Herranz, H., Perez, L., Martin, F.A. and Milan, M. (2008) A wingless-Notch double repression mechanism regulates G1-S transition in the Drosophila wing. EMBO J. 27, 1633-1645.

16. Martinez Arias, A. (2003) Wnts as morphogens? The view from the wing of Drosophila. Nature reviews in Molecular Cell Biology 4, 321-325.

17. Hayward, P., Kalmar, T. Martinez Arias, A. (2008) Wnt/Notch signalling and information processing during development Development 135, 411-424.

Grasping at straws-3

Collection of batches of wing imaginal discs of the indicated ages, determined as hours from egg laying. The blue staining represents the vgQE; compare to Fig 1. As the second instar (L2) happens between 72 and 96 hrs AEL, one can see here that much of the growth of the wing happens at the boundary of the second and third larval instars and that, after half way through the first part of L3, the wing does not grow vert much. The QE, which is a faithful reporter of the wing, only starts at the end middle and the end of L2 (Cassie Yu Bian and AMA)

Acknowledgements: I want to thank three colleagues who have helped me craft this discussion. JP Couso, T. Klein and M. Milan have been helpful and critical on this matter. They have also made contributions to the field and, notably, to the issues raised by this work and both News and Views. It is unfortunate that their work has been forgotten, as it does enlighten and broaden the subject in addition to provide support for the conclusions of Alexandre et al.


On details of mutants, details of timings, details of patterns, details of appendages, details……

These are some comments on the work of Zecca, M., Basler, K. & Struhl, G. Cell 87, 833–844 (1996). Direct and long-range action of a wingless morphogen gradient.

The papers quoted by Struhl (A1, A2) in support of the notion that Wingless acts as a long range morphogen, claim to show that diffusible rather than membrane tethered Wingless could change the levels of expression of presumed targets like Distalless and Vestigial. Two coments on this.

First of all, nobody disputes that Wingless can diffuse and does diffuse during development. The point is whether this diffusion has functional significance. In the experiments  in ref. A1 there are no functional tests so, one cannot conclude much of substance to the arguments from the reported observations. It could be argued that it was shown that Wingless can change the levels of Distalless and Vestigial. Probably, but the observations in this report (I mean what is shown) are questionable as there are few and selected examples. The bulk of the data for this is in Figures 3 and 4. It could be the techniques of the time and the lack of details and controls, but there are many questions on these figures, particularly if they are the best examples in support of the long range actions of Wingless.

In Figure 3, the lasers of the confocal are so high that all constructs appear to have a long range effect. It would have been good to have some controls and cellular resolution, particularly as it is distance from source that is at stake here. Notice, for example, that in 3F there is a lot of ectopic Dll in places where there is no expression of Armadillo (incidentally, it is very difficult to work out what the authors are looking at; not only there is no orientation of the discs –what is anterior or posterior- nor staging, there is no wild type reference for these experiments. Furthermore, the authors do not use the endogenous Dll expression but a Dll-LacZ which does not recapitulate the endogenous expression and appears to be somewhat sensitive to Wingless signalling –unpub. obs-).

Also, to highlight but another example, it is odd that in 3D the ‘long range’ effect of Wingless on Vg is only on one side of the disc (the left) and not on the other (the right). These examples, crucial to the argument, suffice to show that they are not only insufficient but inappropriate for the case. An effect of Wingless on the levels of expression of Vestigial has been shown so, they are right, but the effects of Dll (not the enhancer used here) are more difficult to gauge and this is crucial for the notion of Morphogens.

Figure 4 raises many questions. A look at it shows that the ‘induction’ of neur-Z is very sparse. It is surprising how few cells are led to express it in A, there is very little non-autonomy in C and in E the questions arises why is it that only few cells in the clone express it. Needless to say that once again, as in Fig 3, we do not know what are we looking at: which part of the disc, which stage, etc. This problem with details were at the time, and can be seen now, one of the major issues with this work.

But in the end, accepting that Wingless signalling alters the levels of expression of Vestigial and Distalless, these changes in expression appear to be functionally irrelevant. Although no functional test exists in ref. A1. JP Vincent and his colleagues have shown that removal of the DV stripe of Wingless from the developing disc, does not affect the patterns of Distalles and Vestigial (A3), which fits the earlier observations of the lack of an effect of the stripe of Wingless on the patterning of the wing (A4). There are also other examples which show that Wingless is not necessary for the growth of the wing which should have been discussed. Just to quote one: apterous mutants lack a wing but when they are combined with a mutant for Hairless (a negative regulator of Notch signaling) a wing grows without a margin and without Wingless expression (A5). This phenotype is similar to the one that results from removing the DV stripe of Wingless and reinforces the notion that the DV stripe of Wingless does not act as a source of long range morphogen required for the growth and patterning of the wing but rather as a local signal for neurogenesis at the anterior margin.

The wing is not the only place where Wingless has been made into a Morphogen and some of the early work of Struhl on Wingless deals with the leg (A6). Much less attention has been paid to the patterning of the leg discs, at least in the public domain, but detailed experiments carried on after the work on the wing have not found evidence for a long range patterning activity of Wingless (A7-A10). By now it is well established that in Drosophila, the pattern of the leg is established though a sequence of mutually dependent interactions between gene regulatory networks in a background of Wingless activity. The similarity with the wing disc being uncanny and the relevance of these observations to the findings of Alexandre et al. obvious. Once again, the silencing of these results and their relevance to earlier statements is, at the very least, surprising and reveals Occam’s broom at work.

A most important detail. The work of Zecca et al (A1) has one loss of function experiment in support of the long range action of Wingless in the growth and patterning of the wing. The experiment is shown in Figure 1, particularly panels E and F. The legend reads:

(E and F) Dll (E) and vg (F) expression in wgts wing discs 2 days after a shift to the non permissive temperature: Dll expression in the wing is abolished, and vg expression is reduced to a thin stripe of cells along the DV compartment boundary

The devil might be seriously in the detail here. It is difficult to know when the temperature was shifted as we are not told the age of the discs and this, given the changing patterns of Wingless expression, is crucial to interpret the observations. The experiment is not easy (though there is no description of how it is done so it is difficult to reproduce) since growth at the permissive temperature (18oC) is slower than at 25oC which adds to the difficulty of interpreting the outcome of the experiment. Notwithstanding this, the figure contains some landmarks that allow us some useful inferences.

The leg disc on the left in panel E suggests that the shift must have happened late since the expression of Dll in this disc depends on Wingless early (the authors know this). If the shift had been done early, Dll would have disappeared from both. As it is expressed in the leg, the shift must have taken place at least 48 hours AEL (at 25oC). It should also be pointed out that this disc has a sizeable pouch (gauged from the rings that define the hinge), smaller than wild type but large, which suggest that the shift has been made so late (in the 25oC timeline) that there is little effect on the growth of the wing (although a proper analysis of this depends on timings and stagings that we are not given): as we do not know the age of the disc nor how much time it has been at 25oC (or is it 29oC?) it could well be that the reason for the small size of the wing pouch has to do with the young age of the disc. However, notice that despite this the authors want us to see here lack of growth of the wing. The pattern of Vestigial in F tells us a few more things about this experiment. The pattern shown is surprising, as in the experience of those who have done these experiments, in the absence of Wingless, Vestigial is either gone or present but never maintained in a DV stripe which, by the way, resembles the vestigial Boundary Enhancer (BE) that was first characterized by S Carroll’s lab. So, it could be that for some reason they have uncovered an endogenous pattern that is dependent on the BE which, incidentally, is independent of Wg once it has been activated. Whatever it is and wherever it comes from, this pattern of expression provides another hint of when the shift was done as it suggests that the DV boundary had been formed at the time of the shift (Wingless is necessary for the DV boundary to form properly by regulating the expression of Delta (reviewed in A11). As in E, this places the shift very late since the DV compartment boundary is not established before 48 hours. In this panel, as in E, there is wing pouch and with all the caveats raised above and the lack of detail of how the experiment was done, this would suggest that the shift was done about 72 hrs+  (in the 25oC timeline) and that removal of Wingless at this time, whether it has an effect on Dll and Vestigial or not, it has little effect on the development of the wing, as has been shown before and later (A3, A4).

One added small detail. There is something difficult to understand here, and when one looks for details in the materials and methods, there are none. More significantly, some of us would like to know which wg ts (IL114 allele one presumes) chromosome did the authors use. The reason to ask is because if it is the original one from the Nusslein-Volhard collection, it happens to have an associated lethal which makes this type of experiments impossible –tried and tested in reference 7. In fact this is the reason why in our work (A4) we used different chromosomes and often in trans. As there are no details of how this experiment was done, what chromosomes were used, how the mutants were recognized and what was the timing of the shifts, it is very difficult to understand what is going on. Some details would have been and still would be welcome.


There might be a more fundamental and interesting reason for Struhl’s problems with these results. In particular one that, if true, highlights the limitations of a strict genetic analysis of development. Struhl is, first and foremost, a geneticist; probably one of the best developmental geneticists of the 80s and the 90s. He uses genetics to infer mechanisms following a straightforward method based on the analysis of mutant phenotypes: 1) set up a genetic situation, often clones of gain or loss of function of a particular gene; 2) let the system run its course; 3) obtain a result, usually in the form of a terminal or quasi terminal phenotype, and 4) use the outcome of the experiment, together with a hypothesis, to infer what has happened i.e. what kind of mechanism might lie underneath the observed result. The essence of this method is that it works with a black box which contains the mechanism. The experiments of Alexandre et al. have a similar flavour but have many elements of cell biology and show an interest in understanding, rather than inferring, what is in the black box. Struhl has decided what there is in the black box and therefore, in his view, any result against it (what he believes to be there, simply because it is his favoured explanation) needs to be looked at carefully. He should realize that today we have methods that can crack the black box. Genetics is a beautiful formal intellectual construct which has provided undoubted insights into many processes but it has done best when going hand in hand with other complementary techniques like cell biology or biochemistry. The work of Alexandre, Baena and Vincent does this and, in doing so, advances our understanding of Wingless signaling in development.

So, I would suggest that part of the problem of Struhl has to do with his repeated attempts to use classical and limited techniques and frameworks against more rigorous and modern approaches to the problem.

Appendix References

A1. Zecca, M., Basler, K. & Struhl, G. Cell 87, 833–844 (1996). Direct and long-range action of a wingless morphogen gradient.

A2. Zecca, M. & Struhl, G. (2007) Development 134, 3001-3010. Control of Drosophila wing growth by the vestigial quadrant enhancer.

A3. Piddini E, Vincent JP. (2009) Interpretation of the wingless gradient requires signaling- induced self-inhibition. Cell 136, 296-307.

A4. Couso, J.P., Bishop, S. Martinez Arias, A. (1994). The wingless signalling pathway and the patterning of the wing margin. Development. 120, 621-636.

A5. Klein,T., Seugnet, L., Haenlin, M. and Martinez-Arias, A. (2000).Two different activities of Suppressor of Hairless during wing development in Drosophila. Development 127, 3553-3579

A6. Struhl, G. and Basler, K. (1993) Organizing activity of wingless in Drosophila. Cell 368, 527-540.

A7. Galindo, MI., Bishop, S., Greig, S. and Couso, JP. (2002) Leg patterning driven by proximal-distal interactions and EGFR signaling. Science 297, 258-259.

A8. Campbell, G. (2002) Distalization of the Drosophila leg by graded EGF-receptor activity. Nature 418, 781-785.

A9. Estella C, Voutev R, Mann RS. A dynamic network of morphogens and transcription factors patterns the fly leg. Curr Top Dev Biol. 2012;98:173-98.

A11. Kojima, T. (2004) The mechanism of Drosophila leg along the proximo distal axis. Dev. Growth Diff. 46, 115-129.

A11. Hayward, P., Kalmar, T. Martinez Arias, A. (2008) Wnt/Notch signalling and information processing during development Development 135, 411-424.

Michael Bate and the pioneering of the developmental analysis of neural circuits

Increasingly, the biological sciences bask in short lived small bites of ‘success’ where the publication rather than its content and real impact (as opposed to that of the journals) rules. Highthroughputness, terabytes of information, large genome data analysis, saturation screens, all form part of a culture with little time for pause, reflection and ponder. Perhaps it is because of the prevalence of these attitudes that meetings to celebrate the contributions of senior scientists provide an opportunity to appreciate what it is that we are missing in the current structure of the biological sciences.

On December 14 (2013) a symposium took place in Cambridge on the “specification and development of neural circuitry’ to celebrate the 70th birthday and science of Michael Bate. The meeting, organized by Alicia Hidalgo and Matthias Landgraf, brought together a group of old and young developmental neurobiologists around individuals who had been associated with Mike throughout his career. For those outside the field of Developmental Neurobiology –but not if you live in Europe- it is easy to overlook Mike. His quiet, science centered attitude, far from the limelight, looking at Nature in the face and finding out how it works, contribute to this. But the impact of his work is anything but quiet. His legendary teaching, in particular in Cambridge, Cold Spring Harbor and Bangalore, as well as the many graduate students, postdocs and PIs he has inspired, place him amidst a small group of people with real impact in modern Biology and whose work should be an example to us.

His toilings span over 50 years in a trajectory that when woven together, reveals a unity of direction and content. Much of Biology is about form and function and Mike’s career represents a modern approach to this problem. His lifelong interest has been to understand how neural circuits are put together and whether their development reveals a logic to their function i.e. whether understanding how form arises might not contain insights and reasons about function. To do this he developed over time a rare blend of neuro- and developmental biology. One can see this emerging, in a rather prescient and programmatic manner, in the publications of his PhD thesis, done under the supervision of John Treherne in the Department of Zoology in Cambridge, on the gin trap of a moth and published in the three papers in the Journal of Experimental Biology in 1973. In the introduction to the first paper he lays down his research agenda: “the aim of the present paper is to define a simple case of neuronal differentiation where the techniques already used in the investigation of pattern formation in the insect epidermis might be applied to the mechanisms which regulate the central connections of the epidermal sensilla” (Bate, M. J.Exp. Biol. 1973 59, 109-119). The work is an interesting combination of physiology, theory and some developmental biology, pretty much the combination that would run through his scientific life. Behind the attention to the detail there has always been a big theme laid out by the work of the late D M Wilson who, as Mike pointed out many times, poses questions about our notions of biological design upon pointing out that the flying circuits for the locust are in place before the locust needs to fly (implicitly, before they could have been selected for the function they are being built).

After his PhD, Mike undertook a life of moving around with important stops in Canberra (Australia) and Tubingen (Germany), a time during which he matured his thoughts on how to tackle the problem of the emergence and assembly of neural circuits. In 1976 he produced two seminal pieces of work, one on pioneer neurons (Bate, M. 1976 Nature 260, 54-56) and the other, “Embryogenesis of an insect nervous system. I. A map of the thoracic and abdominal neuoblasts in Locusta migratoria” (Bate, M. 1976 JEEM 35, 107-123). Two years later, he produced a second important paper on the ground plan of the insect nervous system: , “Embryogenesis of an insect nervous system. II. A second class of neuron precursor cells and the origin of intersegmental connectives” (with Grunewald, 1978 JEEM 61, 317-330). These three papers were seminal because of what they established, launched and inspired. A nervous system, at least in the first instance the insect nervous system, was revealed to be built stepwise, making use of cell driven precise and identifiable processes. During the laying down of its ground plan, the central nervous system used identifiable cells that performed defined tasks of pioneering an otherwise blank slate of the tissues through which the axons and the system had to navigate. Cells born afterwards would track those paths and the development of the system could thus be linked to its developmental engineering. The papers were much ahead of their time and conceptually laid the foundations for a long and interesting research agenda. The notion of working with single identified cells to study their behaviour and contributions during development was born and later on when genetics broke the black box that was its molecular underpinning, this work was the foundational reference.

mb1Mike had worked with locust because, as he pointed out many times, the embryos were big and the cells large. This was important as the purpose of the exercise then was to identify the tracks as they were laid down and how these related to cells. So, size mattered for the eyes and for the tools: scalpels, needles, stains and microscopes and, of course, no antibodies, no Gal4 lines that would identify single cells. The consequences of this work were huge and only time puts them in the correct perspective. At this time he entered into an immensely fruitful collaboration with Corey Goodman, one of the people he inspired and led. One important challenge in this collaboration was, as Goodman recalled at the meeting, to get to see the blueprint of the Drosophila nervous system in the embryo. The reason for this was not only one of completeness –observation of the blueprint in
all insects- but the need to hack into Drosophila to take advantage of the powerful genetic tools that were emerging at the time. The difference in size between the two is large –Drosophila is about 20 times smaller than the locust and dealing with this, in pre-antibody
days, required skill and insight. Mike managed to reveal this structure through a combination of his unique skills in dissection and observation and thus led the way to show a conserved body plan for the groundplan of the arthropod nervous system laid out in a landmark paper (“From grasshopper to Drosophila: a common plan for neuronal development” Thomas, JB, Bastiani, M., Bate, M and Goodman, C. 1984 Nature 310, 203 – 207). The path was now laid to use Drosophila to get the molecules and the Goodman lab, as Goodman himself recalled at the meeting, went on overdrive to identify genes and proteins involved in the pathfinding: a stunning collection of genes and mechanisms that were uncovered over the next few years. It could be argued that the genetics of Drosophila would have revealed all this. Maybe. Or most likely not, because while it might have thrown out genes and painted paths, only the slow, thoughtful, careful work that preceded these experiments, created the questions (and they were the right ones) that needed to be addressed by the genetics. A consideration of the watershed work of Goodman’s laboratory highlights that the difficult thing is to know what one wants to know, to map out the right terrain, before one launches into finding out the machine that runs the process. If we do not understand flying we cannot understand the machines that do the flying.

Mike was not directly involved with the opening of the genetic Pandora’s box of axonal pathfinding but without his contribution the content of the box would have been, for a while, just a collection of genes. At this time, in characteristic fashion he went to explore another virgin territory: the muscles. This time directly to Drosophila. Once more with a combination of his best tools – insight, dissections, needles, stains – and looking at what the cells did without the bias of the genetic or molecular analysis, he now uncovered the groundplan of the muscle system in Drosophila (Bate, M. The embryonic development of the larval muscles of Drosophila. 1990 Development 110, 791-804). Once again he opened up a new field of study and, guided by what the embryo told him, he laid down the questions that would be pursued in the future. He uncovered a blueprint based on muscle founder cells which resembled, in many of their abstract properties, the neuroblasts he had mapped earlier, and saw how this plan developed into a pattern where the properties were not just tracks of axons, as in the nervous systems, but the sizes and orientation of the muscles. And in this work, we can see again, the leitmotif of the need to understand development to link form and function: “It may well be that the assignment of these properties to the muscle precursors, like the specification of neuroblasts, depends on prior regionalization……..to understand this process in detail we have now to combine the description given here with a genetic analysis of muscle development”. And this time, he did pursue this himself led by two postdocs Mary Baylies and Mar Ruiz Gomez. But there was more to this work. This was not some explorer going into unknown territory to add to some geography of the insect embryo. What Mike wanted, wants, to understand is the emergence of circuits and their inner functional logic, and the neuromuscular junction provided a basis to think about this. Perhaps there was some functional reason why there are 30 odd neuroblasts and 30 odd muscle precursors. In parallel with the genetic analysis of the muscle system, together with a student Kendal Broadie, in the 90s he began to chart emergence of neural activity during development. Slowly this finally evolved to the emergence of circuits and in a long standing collaboration with Matthias Landgraff, the functional mapping of the development and function of the myotopic map of the Drosophila larva. When looking at his most recent work with the perspective of time it is difficult not to think of the lines from TS Eliot: “and the end of all our exploring will be to arrive where we started and know the place for the first time.”

Perhaps the myotopic map was the goal when looking at the gin trap in the moth. Sometimes our research moves through curious paths and, if one is lucky, one can see that one is close to the place one wanted to be. That this might apply to Mike was much in evidence at the Symposium, where we also had a chance to see the effect that he and his work have had on people. One aspect that became clear in many talks, but particularly in C. Goodman’s. C. Doe’s and J. Truman’s, was how Mike’s career has always been about seeing things and laying down the ground for others before anybody was there or thought of doing that. Like the true enlightening pioneers, only when he revealed something, it was clear to everybody else that it was what they should be looking at. His work also illustrates that, to do this one needs to have the time and the space to look, see and think. One recurrent theme at the meeting was the role that Janelia Farm plays in modern neurobiology. Here, again, one could not help seeing the influence of Mike, as many of the leading people working there are connected to him and the questions on circuitry so elegantly tackled there are related to his work and interests. The question, of course, is whether much of what is true of Drosophila and other insects will be true of vertebrates. Marco Tripodi touched upon this at the meeting. Time will tell. There is much to be learnt but what there is little doubt about is that the methods and intellectual framework laid down by Drosophila will be important in the understanding of vertebrates. The Symposium was closed by Vijay Raghavan, a close friend and collaborator who extolled the contributions of Mike to the development of Drosophila genetics and cell biology in India.

mb2I had the privilege of sharing much time and space with Mike for 13 years in the basement of the Department of Zoology at the University of Cambridge. This was a most important time for me as through our interactions and seeing him at work, it taught me how to ask questions and think about Biology. In all this, amidst much that the passing of time highlights as important there are two specific things that I learnt from Mike, that I cherish and that I try to pass on to the new generations of scientists. The first one is that the pursuit of Science is not about personal visibility, but about developing an ability to see into the system one is studying. That the prize of research does not lie in being seen, but in seeing. That a publication is simply a report of the observations, work in progress, and, more important, part of a thinking process, rather than the goal and a passport for a short lived glory. The impact that he has had on the field and on people has come from what he has done and revealed and not by where he has published. We should all take stock of this. The second thing I learnt is very important and should be at the basis of cell and developmental biology: how to observe. When going to the microscope –or looking at any experiment- one should be prepared to let the system talk. One should listen with ones eyes to what the preparation says and not override this with what one wants to see. There is always more in there than we can see and only letting ourselves be drawn into it, we shall be able to see it. This attitude is the prevalent one in his 1976 and 1990 papers on neuroblasts and muscles and says how much one can learn from this approach. But in the end, like many others, it was listening to him teach and talk that reminded me always, what science should be about. There is little doubt that Mike has created a school, a school of thinking and of watching, and much of this without really planning to do so, simply because of his way to do Science, something that many of us would like to see returned. With the possibilities of today, blended with thought and insight, the results could be enormous.

What emerged from the excellent meeting in Cambridge was a pulsating story of science, developed over time by people working constructively on each other’s ideas through carefully crafted experiments addressing well thought-out questions. Low throughput biology with high content and an impact clearly defined by the careers and research that it has launched.

Happy birthday Mike and, together with many others: thank you.

The Wingless Morphogen: phlogiston in the Drosophila wing imaginal disc

A pdf version of this post is available here.

An excellent recent meeting in Oxford on morphogens (EMBO Morphogen workshop) gave me an opportunity to think about this notion in relation to a molecules and a signalling event I have been watching, sometimes gazing, for a long time: Wnt.

The notion of ‘morphogens’ was introduced by A.M. Turing in his classic paper on the chemical basis of biological pattern formation (1). The thought emerges from the consideration of “masses of tissues which are not growing, but within which certain substances are reacting chemically, and through which they are diffusing.“ The substances, which lead to spatial patterns, are called morphogens, “the word being intended to convey the idea of a form producer” (1). Later this notion was developed further and knocked into its modern shape by L. Wolpert, particularly in his 1969 paper (2), where he introduced rigorous criteria for such substances based on Biology, something that was missing from the original Turing analysis which, incidentally, had a very different aim from the one that it is often associated with: Turing’s work is a proof of principle rather than a theory with specific aims in mind. Ever since Wolpert’s formulation, morphogens came and went until the genetics of model organisms revealed molecules which did fulfil, to a certain degree, the criteria established by Wolpert (2-4). These criteria, as commonly understood and accepted, are that the molecule 1) be distributed in a gradient; 2) the gradient needs to act long range; 3) the concentration gradient needs to be decoded into a number of discrete states in a concentration dependent manner; in the case of Wolpert’s original formulation, this were the colours of the French flag (2). Over the last twenty years three molecules have earned the accolade of morphogens, sensu Wolpert, BMPs, Hedghehogs and Wnts, with others being said to perform this function in particular situations. Most of the crucial experiments have been performed in Drosophila (5-7) and while BMPs and Hedgehogs pass the test with more or less flying colours, Wnts are (as you will see) a different matter.

Wnt proteins are secreted polypeptide which play a signalling role in the Biology of the cell (see note at the end for more information); the only detail that is important here is that the transcriptional effector of Wnts is a complex between ß-catenin and Tcf (8). The notion of Wnts as morphogens is founded on one, and only one, observation: its expression and perceived function during the development of the imaginal discs of Drosophila.

Imaginal discs are groups of cells set aside during embryonic development which grow hidden in the larva until they emerge to form the adult fly during metamorphosis. The development of these groups of cells has been the subject of a great degree of scrutiny over the years and we do have a fairly good understanding of them at the moment. The wings of the fly emerge from the structures called the wing discs sometime in the early stages of larval development (Figure 1). In the context of this note, the important features of the wing primordium are clear in the third larval instar: a large disc of cells which presages the wing bisected in the middle by a stripe of cells expressing Wingless, the Drosophila homologue of Wnt1. The gene being called wingless for the loss of the wing that follows the loss of function of the gene (see Figure right). This stripe bisects the disc into a dorsal and a ventral domain (future sides of the wing), where it has been suggested that it generates nested domains of three genes, from broader to narrower: Vestigial, Distalless and Senseless (9-11). The stripe is first visible when the disc is small (but not when it is very small) and has been blamed for the growth and the patterning of the wing. In fact, it is the presumed activity of this stripe controlling growth and nested gene expression that earned Wingless its morphogen status and that forms the basis for its general understanding as a Morphogen (9-14).

The development of the wing; modified from ref. 20

However, there is a fact: if one removes the stripe of Wingless expression, a wing develops i.e. the stripe of wingless is not required for the development of the wing (15, 16). The removal of the Wingless stripe leads to a defect in the patterning of the cells adjacent
to the stripe of Wingless, but the wing is, for the most part normal.

This observation was first made using a temperature senstive allele of wingless , in the first analysis of the role of Wingless on the development of the wing (15, specially Fig. 5) and was repeated later with modern techniques removing both the ligand and the receptor (16, specially Fig. 1). In all cases, the result was the same, which is a good thing and something one would like to see more of in Drosophila. So, what is going on?

This observation raises two issues, one scientific, the other more in the realm of the sociology of Science. The first one concerns the function of Wingless signalling and, by extension of Wnt signalling in development. This is an interesting matter which has been followed up, away from the morphogen notion, in a number of reviews and discussions and I suggest that, if you are interested, you look at them (17-21; as well see also the two appendices here). The surprising observation (surprising in light of the commonly held view to the opposite) opens many questions though, since one can obtain phenotypes during the development of the wing with some gain of function forms of elements of Wnt signalling (see Suppl Mat in 22) or, more surprisingly, in mosaics of patches of loss of Wingless function in wildtype wings (23). Why is it then that loss of function in the whole wing does not affect growth but in patches it does? There is something interesting here and I am sure that it will be explored; it certainly needs to. The issue of Wnt signalling itself, which is independent of whether it or it is not a morphogen, is also in need of a serious revision (24; you may want to read this in the form of an appendix at the bottom). I could discuss these important matters at length here but will leave this for another occasion (and promise that I shall). The main objective of this post is to bring up this important and, apparently little known fact about the function of (or lack thereof) Wingless in Drosophila.

Early stages of Drosophila wing development; modified from “Molecular Principles of Development” OUP A. Martinez Arias and A. Stewart

The second issue, that of the sociology of science, is more complicated. Why was it (and actually still is) that despite the observation of the lack of function of Wingless on the growth of the wing –at least from the perspective of loss of function-, there was a deluge of papers on Wingless as a Morphogen? How come an important observation took 20 years to be repeated (work was built upon it, though it was ignored e.g 25-27) and instead experiments were done and interpreted in a light that conflicted with the main observations? The number of papers supporting the notion of Wingless as a morphogen in the 1990s is large, but if one looks at the results supporting this notion and the experimental design behind them one can see a degradation of rigour and how an idea can take over the facts. In fact, there was little evidence for the claims of many of these papers (discussed in 25-27) and more parsimonious explanations (e.g 20) were consistently ignored. I guessed the seduction of the morphogen view is too powerful.

What is a matter of concern is that the notions derived from the belief that Wingless is a morphogen that controls and patterns the wing of Drosophila have served as a template for the understanding of Wnt signalling in other systems, where the evidence rather than weak is non existent.

The story of Wingless and the Morphogen is very reminiscent of that of Phlogiston, a substance that was thoughts to be a universal component of most material on earth and which was liberated upon combustion. The problem was that as measurement fuelled the birth of chemistry, the notion emerged that Phlogiston needed to have negative mass-and many people were not bothered by this. Phlogiston gave way to Oxygen, as Priestly and Lavoisier showed later on, which was a more interesting and real explanation for the experimental results. However, while it lasted the notion of Phlogiston provided an implausible and absurd, but obviously satisfactory, explanation for an interesting phenomenon. The Morphogen property of Wingless is the Phlogiston of Developmental Biology. The strange thing about the case of Wingless was (and is) that the evidence was there from the beginning but most people decided to ignore it.

Perhaps this is a reflection of the way Developmental Biology has worked for the last twenty years: mutant>gene>idea>match>paper>new mutant>new gene>epistasis>idea>fact that ignores the experiments. There are notable exceptions, in particular the early development of Drosophila, where the tight interactions between transcription and the processes have led to a deep understanding of the processes involved. However, when it comes to cells, there is much that we need to learn in terms of methods and approaches. Unfortunately, misunderstandings and misinterpretations about Wingless and Wnt signalling are still ongoing (24) and need to be corrected. Fortunately, things are changing in developmental biology and the EMBO workshop in Oxford ushered a new era, more quantitative and analytical. I suspect that this will benefit Wnt signalling as the notion of Wingless as a Morphogen is like Phlogiston was to Oxygen, it obscures something much more interesting that lies behind the observations that I have mentioned above (15, 16).

Epilogue: The trigger for these lines was a talk at the Morphogen meeting in Oxford by one of the old time Wntologists of Drosophila, a prestigious and much acclaimed scientist. After delivering a whole talk on Wingless as a morphogen in the wing, he was asked what he made of the fact that removal of Wingless during the time that it was supposed to act, had not effect on the development of the wing. He said he was not aware of those facts or papers. Of course, why bother with inconvenient facts? I also want to acknowledge the contribution of JP Couso to the notion of Phlogiston in the context of Wingless signalling in Drosophila.

NOTE: For those interested here you have, in pdf form, two essays. One (24) is a primer that I wrote at the request of PLOS Biology about Wnt signalling. It was rejected because, after submission, the editors and the reviewers thought that everything I said was known; judge by yourself: if it is known why is it ignored? I could update it but its essence will remain the same. It contains some of the internal contradictions of the current views of Wnt signalling. The second one (28) is less formal and is a little piece that I wrote for Sean Carroll, after a conversation in which he asked me to summarize for him my thoughts about Wnt signalling. These form the basis for a piece in BioEssays (17). It does contain some jargon but some of you might find it interesting. In terms of wing development, from the perspective of the DV axis, I suggest you read 18, 20, 27 as well as 29-31 and, please, think and do not listen to the mermaid morphogen songs.

Some references

1. Turing, AM. (1952) The Chemical Basis of Morphogenesis. Phil Trans. Roy. Soc. 641, 37-72.

2. Wolpert, L. (1969) Positional information and the spatial pattern of cellular differentiation. J. Theor. Biol. 25, 1-47.

3. Wolpert, L. (1996). One hundred years of positional information. Trends in Genetics. 12, 359- 364.

4. Ashe HL, Briscoe J. (2006)* The interpretation of morphogen gradients. Development 133, 385-394.

5. Zecca M, Basler K, Struhl G. (1995) Sequential organizing activities of engrailed, hedgehog and decapentaplegic in the Drosophila wing. Development 121, 2265-2278.

6. Lecuit T, Brook WJ, Ng M, Calleja M, Sun H, Cohen SM. (1996) Two distinct mechanisms for long range patterning by Decapentaplegic in the Drosophila wing. Nature 381, 387-393. Erratum in: Nature 1996 Jul 4;382(6586):93.

7. Struhl G, Basler K. (1996) Direct and long-range action of a DPP morphogen gradient. Cell 85, 357-368.
8. Clevers H, Nusse R. (2012) Wnt/β-catenin signaling and disease. Cell 149, 1192-205.

9. Struhl G, Basler K. (1993) Organizing activity of wingless protein in Drosophila. Cell 26, 527- 540.

10. Zecca M, Basler K, Struhl G. (1996) Direct and longe-range action of a wingless morphogen gradient. Cell 87, 833-844.

11. Neumann CJ, Cohen SM. (1997) Long range action of Wingless organizes the dorsal-ventral axis of the Drosophila wing. Development 124, 871-880.

12. Strigini M, Cohen SM. (1999) Formation of morphogen gradients in the Drosophila wing. Semin Cell Dev Biol. 10, 335-344.

13. Swarup S, Verheyen EM. (2012) Wnt/Wingless signalling in Drosophila. Cold Spring Harb Perspect Biol. 2012 Jun 1;4(6). doi:pii: a007930. 10.1101/cshperspect.a007930.

14. Giraldez AJ, Cohen SM. (2003) Wingless and Notch signaling provide cell survival cues and control cell proliferation during wing development. Development 130, :6533-6543.

15. Couso, J.P., Bishop, S. Martinez Arias, A. (1994). The wingless signalling pathway and the patterning of the wing margin. Development. 120, 621-636.

16. Piddini E, Vincent JP. (2009) Interpretation of the wingless gradient requires signaling- induced self-inhibition. Cell 136, 296-307.

17. Muñoz Descalzo, S., de Navascues, J. Martinez Arias, A. (2012) Wnt/Noch signaling: an integrated mechanism regulating transitions between cell states. Bioessays 34, 110-118.

18. Hayward, P., Kalmar, T. Martinez Arias, A. (2008) Wnt/Notch signalling and information processing during development Development 135, 411-424.

19. Martinez Arias, A. Hayward, P. (2006) Filtering transcriptional noise during development: concepts and mechanisms. Nature Reviews Genetics 7, 34-44.

20. Martinez Arias, A. (2003) Wnts as morphogens? The view from the wing of Drosophila. Nature reviews in Molecular Cell Biology 4, 321-325.

21. Martinez Arias, A. (2000). The informational content of gradients of Wnt proteins. Science STKE. www.stke.org/cgi/content full/OC_sigtrans;2000/43/pe1

22. Muñoz Descalzo, S., Tkocz, K., Balayo, T and Martinez Arias, A. (2011) Modulation of the ligand independent traffic of Notch by Axin and APC contributes to the activation of Armadillo/ß-catenin in Drosophila. Development 138, 1501-1506.

23 Baena-Lopez LA, Franch-Marro X, Vincent JP. (2009) Wingless promotes proliferative growth in a gradient-independent manner. Sci Signal. 2009 Oct 6;2(91):ra60. doi: 10.1126/scisignal.2000360.

24. Martinez Arias, A. Wnt/ß-catenin signalling 2.0: making sense of the facts. In AMA Blog (http://amapress.gen.cam.ac.uk/). Appendix attached. Download here

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28. Thoughts on the function of Wnt signalling (for Sean Carroll) Download here

29. Zecca M, Struhl G (2010) A feed-forward circuit linking wingless, fat-dachsous signaling, and the warts-hippo pathway to Drosophila wing growth. PLoS Biol. 2010 Jun 1;8(6):e1000386. doi: 10.1371/journal.pbio.1000386.

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Searching for the inner structure of biological systems; an ongoing quest

An address to PhD students from NIMR and UCL at Mill Hill (London, UK) 16 May 2013. There is pdf version of this post here.

 “It is difficult and often impossible to judge the value of a problem correctly in advance; for the final award depends upon the gain which science obtains from the problem. Nevertheless we can ask whether there are general criteria which mark a good mathematical problem……. A mathematical problem should be difficult in order to entice us, yet not completely inaccessible, lest it mock at our efforts. It should be to us a guide post on the mazy paths to hidden truths, and ultimately a reminder of our pleasure in the successful solution”

(D. Hilbert; Mathematical Problems. Address delivered to II International congress of mathematicians; Paris 1900).

In 1684 Edmund Halley went to Cambridge to try to get Isaac Newton interested in a dispute he had been having with Christopher Wren and Robert Hooke on whether the elliptical orbits of the planets could be explained by a force inversely proportional to the square of the distance from a center. Newton claimed to have solved the problem but could not find the papers so he sent him back to London and promised to do again the calculations. This got Newton going and within 16 months he produced his Principia in which he went beyond solving the ‘small’ problem of the elliptical orbits. Curiously I am told that, as it happens, the Principia do not contain the proof that Halley had asked for. Newton was just pouring into paper what he had been thinking and worrying about and sharing it with the world. And, of course, almost two hundred years later we have a similar episode when Charles Darwin receives a letter from some Alfred R Wallace from Indonesia with an explanation for the origin of species which kicks him into action to deliver his own, very similar but longer developed solution, of the same problem.

What these two well known stories have in common is that the people involved, all household names, were doing what they were doing for sport, for fun. Surely they cared about priority of discovery and competition (witness the bitter arguments between Newton and Leibnitz on Calculus or the gentle manoeuvring of Darwin’s friends with Wallace), but the thrust behind their work was that they loved it, they were driven by a natural inner curiosity and pursued Knowledge. They were not motivated by impact factors, careers or the Warholian fifteen minutes of fame afforded by a high impact publication. They genuinely valued and wanted to find out the workings of Nature and then, when they were ready, tell the world i.e. to publish (for an interesting perspective on Science, have a look at the collection of vignettes from Feynman’s “the pleasure of finding things out” BBC http://bbc.in/12m5F2T and for the whole thing: http://bit.ly/dJ0tia). It is not an accident that the questions these people asked were difficult, things that when known would and did, transform the world. But things have changed and in particular the last twenty years have seen a dramatic transformation of the fabric and the outer look of science, particularly the biomedical sciences. The pursue of knowledge has given way to the pursue of the publication and the significance of the finding is blurred by the impact of the journal in which the work is published. We have lost some perspective about what it is that we do, and most of the time we do not know why we do Science; also nobody asks us. This in part is the fault of my generation. The situation has changed too quickly and by the time we feel the consequences we find ourselves trapped in a very tangled web. The good news is that there is YOU and that that the future belongs to YOU –there is no more powerful weapon than having the future in ones hands- and this is why people like me have faith in you, not only to deliver the answer to many of the questions that some of us know lurk in the background of our falsely perceived knowledge of Nature, but also to create a different and better structure for the way we go about this quest. We also have a duty to guide you through the path to the solution ensuring that you do not make the mistakes that we have made. I shall come back to this but for now, allow me to thank you for the invitation.

It is a privilege to be here and to have the opportunity to share the day with you. There are few things more exciting for someone like me than to spend time with the likes of you, listening to your talks, to your interests and insights. So, THANK YOU. Natalie asked me to talk about my career path, particularly the choices I have made to get to wherever it is that I am. I shall be happy to tell you some of these. However, I want to tell you that they are not helpful to you. It would be foolish for me to suggest (as I have seen some of my colleagues do) that what I or they did, will work for you. The stage on which you operate is different. The world I made most of my decisions that took me here does not exist and was very far removed from the world of YouTube, Twitter, Impact Factors and hot publications…….as you will see. However, there might be something to learn from a reflection of those choices in today’s world. After all, we do have one thing in common: the excitement of finding out things about Nature and it is for this reason that I shall focus the choices on this common bond between us, the passion for Science.  In the end, though, a most important thing today is to hear YOU and I look forward to questions you may have which might make this more interesting.

The first message I want to give you is that Science is something you have to love, something that either you have within you or you don’t. You can learn science but a scientist is something that either you are or you aren’t. Most people doing Science are not scientists, even if they are successful. Do not be surprised; if you think about it you will see that it is true. But let me step back. Taking this premise on board we can move on.

I come from Spain and grew up in a country and at a time where and when education was not valued. We were taught to read and write, had to memorize a lot of facts but, beyond this, you had to fend for yourself. There were no expectations about doing a PhD (what?), there were no goals other than the need to find a job and lead a good family life-and believe me, these are important values. This circumstance has good and bad elements associated with it. On the one hand it leads you to think on your own, to have an open mind and therefore to define your own questions, to shape your own view of the world. On the other hand there is no training, no predefined challenges nor a necessary intellectual discipline early on, like most of you have got. And this has its consequences: gaps which I have been trying to fill ever since. Somehow I decided to study Biology and from the beginning was captivated by Biochemistry, Genetics, the problems associated with the emergence of Life and, in particular, what we call Developmental Biology which in those days was Embryology. At some point two books felt into my hands: Jacques Monod’s “Chance and Necessity” and Conrad H. Waddington’s (yes of the Waddington landscape) compendium “Towards a theoretical biology”. Both stimulated me in convergent ways. Monod’s book made me think very seriously about biological systems as chemical machines. It is interesting that Monod promises in the book a treaty on molecular cybernetics which, unfortunately he never delivered. “Towards a theoretical biology” led me to consider something which, in those days, was not possible –though I did not know. “Towards a theoretical biology” is a summary of a series of conferences organized by Waddington on the thought of the title: the possibility of a theoretical framework for Biology, which took hold of my ignorance. Bored by Botany and Zoology (the way they were taught in Spain) I had become interested in physical and organic Chemistry and was very impacted by the beauty of the logic and organization of Chemistry. If Chemistry was Physics and Biochemistry underpinned Genetics and Cell Biology, could one not work out Biology from Chemistry?……..perhaps….one could find some Physical principles in Biology…… I decided to try to learn some physics and some maths…..but it was too late…..and for theory in Biology, it was too early. Still, these readings sew a seed that has been with me all my life.

At the end of my undergraduate and military duties, I got a chance to do a PhD in the US and went to The University of Chicago (USA), a place with a history on Theory in Biology. Inadvertently this was a good choice and the reason is the one thing I learnt then which I share with you: in our trade, the choice of where to work is very important. Not the person to work with/for/under/over, but the place, and it is a good thing to choose one (if you can, and I think you all can) that has a lot going on because if something goes wrong in your first choice, you have a lot to choose from around. This was important to me because ….things did go wrong in Chicago. What I wanted to do was to develop a Theoretical Biology with a strong basis in Physical Chemistry but….in Spain nobody had told me that we did not know enough Biology for this and that for Theory to emerge you need facts, experimental results, not only ideas…….in some ways Science, Biology in particular, is the story of beautiful theories turned into ashes by ugly facts. And it was the dearth of and scorn for facts that is at the heart of the failure of that Theoretical Biology. Nonetheless three good notions came up from the Waddington exercise: Positional Information, Waddington’s epigenetic landscape  and the clock and wavefront model for somitogenesis. All grew out of the need to frame experiments and the first two of these have been important in my life but in the 70s there were just ideas. So, admitting that I had made a mistake, I opened my eyes and my ears, and learnt that indeed, we did not know much about the building blocks of development……we did know about metabolism, and I have to admit that, as I have said, I did love the intersection of Chemistry and Life…..but as we know today, development is not JUST about metabolism. In the late 70s all was up for grabs, the molecular underpinning of developmental processes beckoned.  And thus, two years into my PhD I realized that I had made a mistake and began to do ‘proper Biology’, experiments. Nonetheless my toilings those two years had not been in vain. I had learnt about Turing, very importantly about Statistical Mechanics but realized that in order to apply all this to development, one needed to learn about the fabric of Developmental systems and this was on the way. I began to appreciate Genetics, did a PhD in molecular genetics and in the course of this work I saw Ed Lewis’s paper on bithorax and what is now known as the “Nüsslein Volhard screen”. Both were interesting, more than that and as I was beginning to think about Genetics, both challenged me and pointed out concepts that have been developed over the years since: programmes, tools, structure in systems.

So, I forgot about Physics and Biology and after completing a PhD on something which I was not too interested in, but which taught me a lot about Biology (at the height of molecular genetics), I came to the UK and spent the next twenty years chasing genes and their interactions in Drosophila. Probing how their functions map to different aspects of development and struggling to understand how and what it is that they control. I have not been a main player in all this but have been fortunate, very fortunate, to do this work at a time where lots was happening, when every month we learnt something knew about what drove a particular process. I also have been lucky to work with talented and inspiring people, people like Phil Ingham, Michael Akam, Peter Lawrence and in particular Michael Bate. But also Postdocs and students, many of who have taught me a great deal. And here a piece of advice, you need to talk to interesting people. Your supervisor is, sometimes, important but need not be the center of your intellectual life. Both as a student and a postdoc I always found mentors, gurus, interesting people who were always happy to have a cup of coffee or a chat and who opened my mind to much that was and is both important and interesting. It’s one of the privileges of our job that many people do not exploit: the freedom to interact with people and to learn from them.

The 80s and the 90s was the time in which mutants turned into genes and genes into patterns of expression and it was left to us, in an exercise which I have sometimes called ‘palm reading’ to use Genetics to get back from here to function, to integrated function. Those years were a very good time to work in Drosophila because it was the best organism to learn about development and I did it in a place, the LMB, where the C. elegans tradition had laid out the same basis about development and how to do this. The fact that Drosophila and C. elegans developed in parallel was important for me to behold and learn from. Genetics lifted the veil of mystery surrounding the connection between genes and development. My main interest throughout this time was the integration of information and this led me to work on the interactions between Notch and Wnt signalling which have taken and will take a lot of my time and attention. But this is a different story which you can follow in my publications, if you so choose.

By the end of the 90s we, as a community, had a pretty good idea of the make up of living systems and of the molecular devices which drive development. The genetics of model organisms had yielded a remarkable picture of conserved transcription factors and signalling molecules, with some exciting puzzles like the Homeobox (which still remains a puzzle). The zebra fish and the mouse were following in the footsteps of these organisms and were beginning to open up their secrets. A universality of plan at the genetic level was emerging. In many ways, by the end of this time, one could agree with Stephen J. Gould that ‘for sheer excitement, Evolution as an empirical reality, beats any myth of human origins by light years. A genealogical nexus stretching back nearly a billion years and now ranging from bacteria…to the highest Redwood tree, to human footprints in the moon. Can any tale of Zeus or Wotan top this? When truth value and visceral thrill thus combine then, indeed, as Darwin stated in closing his great book, there is grandeur in this view of life” (SJ Gould, Science 1999; 284, 2087 Darwin’s more stately mansion).

But, what did we know about the function of all these genes? How did they make a cell, let alone an organism? How did it all work together? We did know the alphabet, but did we (do we) know the syntax? We have the parts, but how do they come together into a functional whole? Genetics has been an amazing tool of discovery but, alone and in the manner that we have used it so far, it might not be the tool of choice to see how a cell actually works not even how it is functionally organized (two comments on this: http://bit.ly/10fZkmK and http://bit.ly/185sZp5). It seems to me that we have not risen to the challenge and that for the last ten years we have been bootstrapping a collection of parts that has a collectionist, rather than an engineer, flavour to it. How can we progress? Biological systems not only produce the attractive patterns that seduce us, they also produce numbers and rhythms: think of the way homeostasis of a tissue like the skin or the blood works, think of how your two arms (which have never been in touch) grow to pretty much the same distance and with the same proportions, think of the time course of events which are the same in you and in me. Can genes produce these numbers? Sure they are ‘encoded’ in the genes but, how are they decoded?

While learning genetics with Drosophila, I had been following pieces of work that tackle the behaviour of single cells and at this I would like to mention the work of Tariq Enver who probably was the first person to realize that the behaviour of single cells could be different to that of their ensembles. The reason why this was important lay in the principles of statistical mechanics which saw the properties of an ensemble as a result of the statistical averaging of large populations of its components. Around the year 2000 I had the good fortune of attending a small conference at Les Treilles in Provence, where I heard two talks that had a big impact on me. One was by Michael Elowitz, the other one by James Ferrell. I was “bowled over”.  Elowitz’s talk was about noise in gene expression in bacterial systems, Ferrell’s on the behaviour of signalling systems at the level of single cells. Both contained a mixture of theory and experiment that I had yearned for. Both emphasized the importance of measurements and of how to use measurements, detailed measurements, to guide our thinking. At the same meeting, Ernst Stelzer (of confocal microscopy fame) made a statement which has followed me since: biologists, he said, do not know how to make a measurement and this is most obvious in their (our) failure to distinguish between an average and a distribution. It is true and, understanding this will change your view of biology. We have made a science of averages while the information lies in the distributions. All together, the three days at Les Treilles changed my mind, again, and reminded me of my interest to piece together life, development from its components. A statistical mechanical approach to Biology was not possible in the late 70s, but perhaps now, it was. I decided to try to think along the lines of Elowitz, Ferrell and others, in particular Leibler and Alon, and see if this had something to do with development. But, was Drosophila the system to pursue this? The answer was no.

I wanted a system in which one could collect data at the level of single cells, where we could record events over time and which, if possible, could have genetics. Furthermore, if it was simple, this would be great. Embryonic Stem (ES) cells have provided me with such a system and over the last few years, together with a very talented group of people, we have been probing what I would like to call the “inner structure of biological systems”. It is early days, but I believe that they, ES cells, are a good system to gain insights into this as a guide to the inner structure of biological systems. They allow measurements of just about anything you want to measure at the level of single cells, they allow averaging and dynamic analysis, they make choices that follow those that cells make in embryos and they represent the challenge of using them to reconstruct organs and embryos. They offer the possibility of realizing a statistical mechanics of biological systems; from component elements (molecular devices) to macroscopic variables (phenotype).

However, where we seach for those laws, principles, whatever, is not relevant. Each of us might have our favourite system. What we need to do is to acknowledge that the aim at the moment is not ONLY to gather more components, but to put them together and to look for quantitative targets. We need to change our mindset because we want to follow Richard Feynman and build systems in order to show that we understand them. To do this we need to penetrate their inner functional structure which is not just a collection of pieces. To see what is happening I would like to remind you of the story of Treasure Island. As it turns out, Robert L. Stevenson wrote Treasure Island around a map, which his nephew and he had been drawing. When the book was finished, he sent it to London for printing but he sent the map separately. The book made it, the map did not. He wanted the map and not having a copy, he had to infer it from the narrative. This was frustrating as he knew that whatever he did, the original map never produced itself. This is exactly the situation that we faced in Biology, particularly Developmental Biology. We have an advantage over Stevenson, though we do not have the map, we have its outcome: the cell, the organism. And we can see that the map that the narrative of Genetics produces, never matches the blueprint that produces a neuron or a rose (for an extended version of this idea, see “Maps: resolution and insight in Biology http://bit.ly/11JnvBF).

I cannot end up without addressing the current structure of Science, in particular of the Life sciences. The reason to do this is because it affects you and because, as I said at the beginning, you have the opportunity –if not the power- to change it. It is a measure of where we are that today in order to do Research, it is not enough to have good questions or interesting answers, that you, me, us, need to consider the framework within which we work, that we need to ‘sell our projects’ to ‘pitch them’ and therefore we need to be part salespeople. Sure this has happened before, but then there was room for the scientist who lacked those skills. Not today. Research has become expensive, the funds are not easy to get and basic research is difficult to justify. Furthermore, we have conflated content with impact and fashion, have confused intellectual potential with the glitter of certain publications on which we rely to gauge the ‘short term’ value of our work. This has consequences and I am afraid that half or more of you might not survive in this environment so: be careful. Change will come but will come slowly. The pace will depend very much on you and whether you choose to stick to the methods that we have created for you or to move forward and live with the times. The problem, the main problem, is that we are working within a structure from another time, catering for other needs, which has grown without adapting and now is making water. The methods of funding, of selection for jobs, above all the procedures of presenting and publishing our results belong to the 60s and the 70s but the materials we work on and the environment is not the same. Surely we need to adapt too (see the interesting posting http://bit.ly/U423za from Casey Bergman on scientific growth in the XX century) but we are not doing it. Music, literature, journalism have been changed by the web but we only use the web to make our work more cumbersome. We need imagination, we need you to take what is good from us and turn it into something that works for everybody. I have seen very bright people, real scentists, quit and I do not like this.

Notice that the system that we have is one that has worked for….. those who created it and run it …but it is making water and we need to change it. Open Access is a good thing but, Peer Review, the evaluation of impact, the organization or research teams, the connection between basic and applied research, the relationship between Universities and Research Institutes, these are THE issues that need addressing. We will address them…however, while we get there, you can contribute with your choices, with your attitudes. Remember, or let me tell you, that you are the privileged ones and that with privilege comes responsibility. Many of you will lead the future and I would encourage you to lead change because though Science has an important individual component, it is today more than ever, a team work.

Never compromise your principles and interests for short term gains. Remember that the real prize does not lie in the accolades that you receive but in the joy, the wonder of seeing something for the first time and even better, to know, that it might be important. As the pianist Glenn Gould said about Art, I say about Science, it should not be “the release of a momentary ejection of adrenaline but the lifelong construction of a state of wonder and serenity”.

Some people like to look back with nostalgia and think that their time, that in which they were your age was very good, the best. There might be some truth in this in so far as those times the community was small, our ignorance large and the questions few and well defined. But I would say the situation now is better; we know more and we can know more. There was a golden age for uncovering the pieces, there is now the golden age to put them together. Remember because we know the components we do not know how they work together. I shall not abound on metaphores about this. Instead, let me tell you a few problems (in the spirit of Hilbert in the opening quotation) of problems that are both important and interesting, in developmental biology. Furthermore, they are open. Here you have them:

  • What is the scale of biological processes? how many molecules are involved in specific processes? What are the time scales of molecular and cellular events? We need to measure.
  • There is an intuition that biological systems are hierarchically organized but we know little about this structure. What are the networks, the functional networks of the cell? How are they linked at different levels (molecular to cellular)?
  • How do cells generate time? We do know a bit about this from the circadian clocks but there are other clocks associated with homeostasis and dynamics associated with development.
  • What is the role that mechanotransduction plays in development? How do cells sense and react to density?
  • What is the relationship between the programme and the organism.

Key in the work towards the answer to these problems is the need to measure, to be precise in the design and execution of the experiment, to have quantitative predictions. Biology needs to change and become more quantitative.

I shall finish where I started. You have the most powerful weapon that you can have: the future in your hands, the future in your future. You live at a time when you are empowered by technology to find, just about anything you want to find out, and by the internet to develop new, efficient, useful and fair ways of disseminating your findings.  Be creative ad brave. And to this add that a most important thing in Science is to have a good question. Today, though, you need to have a pragmatic approach, you need to do something that will allow you to survive and which does not distance you from your interest, but do not forget that interest, that passion. One of my colleagues said once: I do not have interests, I have passions. He was/is a scientist. Never forget that the real reward, the real prize is not a paper in Cell, Nature or Science, but the actual thrill of finding something new and interesting, to peer through an experiment and see, for the first time, something about Nature that was hidden before you saw it. If you are a scientist, you will recognize that moment. Do not let anything destroy it. Treasure it. It is the only thing that nobody will take away from you. When things get tough, and they will, get back to it to remember what all is about. Ah, and help us change this so that, though in a different manner, Science can regain its rightful value and place.

Appendix to “What do genetic screens tell us about the inner structure of biological systems in developmental and cell biology”

Outline of a proposal for the inner structure of the cell: an interactive project.

Here I would like to put forward a seed for a framework to think about the ‘inner structure of the cell” which should help framing the outcome of genetic screens. S. Brenner has talked about the inner representation of an organism when referring to the manner in which its different parts, its development are encoded in the genome. I would argue that in order for this notion to be useful and to be useful in the use of Genetics to unravel it (see the companion piece ), we need to tackle the functional organization of the cell; its physiology. I want to stress that this is a seed that it is hoped to grow through interactions and comments from all of you. If you have any and want to participate with information and ideas, write to ama11@hermes.cam.ac.uk. Maybe we can work together in an interactive project.

Instead of a multiply connected interactome view, it is suggested that the cell is organized hierarchically with four levels that, at a higher level, integrate development with the biology of the cell (Figs 1-7).


Figure 1. At the core of the system there is a relatively small number of Gene Regulatory Networks (GRNs) organized into network motifs, configuring a collection of Information Processing Units (IPUs) that interact with each other through some of their component elements in a cell type specific manner. The networks will be cell type or developmental stage specific and many will share some of the elements. These GRNs are of the kind that have been discussed by U. Alon, M. Elowitz and colleagues; they have the intrinsic property of generating temporal patterns of activity and, through interconnections and the feedback of downstream elements, to generate programmes of gene expression. In some cases the networks are cell type specific (e.g mesoderm, endoderm, neural…….) in others the same elements are connected in different manners in different cell types. Thus, cell types, high in a developmental hierarchy, are specified by specific networks linked through particular connectivities of existing networks. This structure allows for these IPUs to rewire themselves within and between each other. In all cases the connections have variable strengths, are dynamic, and are subject to biochemical fluctuations (see Trott et al. 2012 for an example of these notions at work).

Figure 2. The core of IPUs is encapsulated in a signalling environment made up of Signal Transduction Networks (STNs) which has a more loose structure but which nevertheless is constrained (in terms of interactions). The activity of this STN layer looks at the collection of IUPs from which it also receives inputs to form a Core Information Processing Center (CIPC), which is likely to be cell type specific. With cell type not meaning ‘terminally differentiated” cell type. The interaction between STNs and IPUs endows individual cells with specific phenotypes; the fluctuations derived from the chemical nature of the connectivity generates expression heterogeneities, which have been described and which become very important in transitions between cell states or cell fates. Signalling contains two kinds of functional units: some that control the connectivity between and within the individual GRNs, and those that regulate the strength of the interactions between the nodes (in the past we have suggested that Wnt and Notch signalling are involved in this activity see Martinez Arias and Hayward, 2006). The interactions between these two levels (IUPs and STNs) are, like those between the elements of the IUPs, plastic and cell type specific but probably affect ALL cell types i.e. the CIPC is a dynamic structure.

Figure 3. There is now a discontinuity between this Central Core (CIPC) and the next level (Peripheral Information Activity Center) which is made up of two components: one not cell specific composed of the basic cellular General Machinery (cGM) and some circuits (TM for Transducer Modules, protein circuits in this case) which act as interphases between the environment, the CIPC and the PIAC.

Figure 4, 5. At the heart of the outer layer, there is a collection of modules (TM) whose function is to take information from the outside (or the CIPC inside) and link it to module specific cellular General Machinery (cell cycle, cytoskeleton, traffic…..see Fig.4 for a list). Thus, the TMs lead to a cell type integration of the cGM into cell type specific activities. An example what is meant by this is provided by the module known as Planar Cell Polarity (PCP) pathway. In this view, PCP is a molecular device used to translate extracellular cues (chemical and mechanical) into the cytoskeleton, and is cell type specific i.e its components are shuffled and organized in a cell type specific manner. Equivalent modules can be found for transcription (in particular certain chromatin remodellers and the Mediator complex are likely to mediate this function), traffic, adhesion, cell cycle…the staples of the cells. The prediction from this speculation is that there will be other modules in addition to PCP performing equivalent functions. Furthermore, it is likely (and there is already evidence for this) that some of the elements of the PCP module will bridge with adhesion and traffic. Each TM being associated with a function. A second important function of these TM modules is to channel information between cGM and the central CIPC core and this is achieved through its links, direct or indirect, with the signalling space (Fig. 5). These outer layers (PIAC) have a high degree of redundancy and plasticity derived from extensive element sharing.

Figure 6. Thus, The TMs are at the heart of the functional definition of a cell type or state, as indicated in this diagram.

Figure 7. This highly speculative organization of the inner structure of the cell could account for the outcome of genetic screens. Thus, one would say that the early genetic screens in the 80s and 90s identified many of the components of CIPC, because they were looking at global compounded phenotypes (body plan, presence or absence of organs or structures, loss of cell identities early in development which would have knock on effects on the general structure of the organism e.g mutations in major signalling pathways or common elements of GRNs). The screens did not target connectivity or structure thus we really do not know much about this. We know something about cell type composition i.e. what elements correspond to which lineage or which cell, but not structure. As the screens get refined they target elements of the higher levels, the TMxs or the results of losing elements in T and GM. There is a very high degree of genetic redundancy in both levels, associated with the plasticity of the system and therefore, the phenotypes can be more subtle.

Problems and issues for discussion: This is very general but it might be useful as a start. Perhaps it could be a good idea to apply it to a specific problem, cell type or developmental system. But its value is that it should be helpful in explaining the outcome of genetic experiments in a general manner.



Martinez Arias, A. and Hayward, P. (2006) Filtering transcriptional noise during development: concepts and mechanisms. Nat. Rev. Genet. 7(1):34-44.

Trott, J., Hayashi, S., Surani, A., Babu, M. and Martinez Arias, A. (2012) Dissecting ensemble networks in ES cell populations reveals microheterogeneity underlying pluripotency. Mol Biosyst. 8(3):744-752.

What do genetic screens tell us about the inner structure of biological systems in developmental and cell biology?

NOTE: This is not a review (this is not the place for such things). This is a commentary, a couple of rough notes unpolished and free in style, an attempt to generate discussion and debate, of pouring out some thoughts. One important thing,  in case you reach the end: I believe what I say here. It is likely that this will evolve. If you have any thoughts or comments, do not hesitate to contact me (ama11@hermes.cam.ac.uk). A PDF version of this can be downloaded from here.

“We are confronted by a nonlinear system the theory of which is fragmentary, complex and confused” (F. Crick talking in 2003)

A physicist’s thought: difficult business Biology. ………..

Sometimes I wonder if we have not lost the plot or maybe, as we have been told a number of times, whether Biology is just ‘different’……different from, for example, Physics. I guess this comes from the fact that much of modern Science likes to be modelled on Physics and some of us just suffer from Physics envy. Well…..perhaps Biology is indeed different. The differences between physical and biological systems have been dissected in a few (not many) interesting pieces (Hartwell et al. 1999; Gunawardena, 2012;  Roth 2011) and it is important to bear them in mind when thinking not only about what we want to know, but also about how we want to go about finding out what we want to know and, more important, what we should accept as an explanation. The second issue, the methodological one, is the main issue here.

What we want to know is how living systems work, how they are organized and structured. This for two reasons: to know and, also, to harness this knowledge to improve our quality of life. The leading light in this process of discovery has been, is, and will continue to be Genetics and there are good reasons for this. Through a combination of imagination and logic, the realization that phenotypic defects are associated with mutations in specific genes and that one can use molecular biology to find out what those genes code for, and Biochemistry and Cell Biology to learn how their products work, has allowed us to build a logic and a formidable technical and intellectual arsenal that underpins our current image of living systems. In terms of the basic processes (metabolism, replication, transcription and translation) this picture sort of works, by which I mean that we can harness it for our interests; whether it is to make better (or different) wine or to engineer insulin. But at other levels, things are still a long way to prove useful and these ‘things’ are important to.

The tools of genetics (classical or molecular) are simple: mutation, phenotypic analysis, epistases and interpretation and synthesis of the results. At the heart of these there are ‘screens’ and it is the nature of screens and their value in today’s science that I want to address here. Screens have become extremely prevalent in biological research but I believe that nowadays they are double-edged swords. If properly conceived and set, they can (they might) tell us something useful about the process of interest. However, nowadays, most of the time they return two answers: either more components of the cell which we cannot place into any framework, or the response of the system to a complicated situation, an adaptive response. Biological systems are, by their nature, reactive i.e. they will always respond to selection and therefore a genetic screen, which by nature is a selective process, will always work i.e. produce, as it should, mutants but….will it teach us something new, interesting, useful or….will it just say that the system responds to our treatment?

The origin and meaning of word ‘screen’ and of the notion of a ‘genetic screen’

Let us go back one step. What is a genetic screen? The term ‘screen’ is derived from the acception of a screen (according to www.thefreedictionary.com: A coarse sieve used for sifting out fine particles, as of sand, gravel, or coal) which then, of course, gives rise to the term to screen (same source: To separate or sift out (fine particles of sand, for example) by means of a sieve or screen). So, the sieve or screen creates a criterion to select for something wanted. Humans have been unconsciously screening genetically for thousands of years, and farmers in particular have been doing this consciously for a long time, as this is how we have got our crops and domestic animals. In many ways, the initial studies of heredity were very closely linked to this type of screen and it is probably not surprising that Mendel was working with crops of the kinds that farmers played with. Nevertheless it was probably TH Morgan who set out to do a genetic screen consciously, when he began to grow Drosophila looking for spontaneous large phenotypic changes, mutations (Allen 1978). He spent over two years looking for some discontinuous change in the outer appearance of the fly, without much joy; collecting small variations until he found white. The rest, as they say, is History and Drosophila became the darling of the mutant hunts, or screens, for many years. Mouse genetics, though with a recent history anchored in tumour biology (Paigen, 2003) also has its roots in breeders of their phenotypic aspects: the fancy mice breeders in the Orient which provided a basis for the research strains that would become popular later (http://research.jax.org/mousegenetics/development/history.html and http://www.hhmi.org/genesweshare/d110.html).  The discovery that radiation and chemicals could induce mutations, changed the way mutants were isolated and the rate at which they appeared and were collected increased (Carlson 2004).

The ability to induce mutations changed the game and the notion of a screen; a directed selection of certain kind of mutants, began to take shape. Phage, E. coli and yeast benefitted very much from this and in this manner we learnt about the metabolic pathways, the genetic code and the basic processes of information transfer in living systems. This knowledge was gathered through mutant screens, which targeted particular processes and used mutants and double mutants to unravel them. These screens were very successful because the questions they asked (a screen always asks a question to the organism) were very targeted and the design was such that one always asked for rare events whose occurrence would be determinant and informative of the process in question. Thus, in these organisms one could screen >106 individuals, which is key on these rare events. This work created the foundation of Molecular Biology (read “The eigth day of creation” by HF Judson for a great account). In parallel, genetics had been applied, albeit in a small scale, to more complex processes, in particular the cell and developmental biology of organisms. However, the lack of clear questions and the difficulty of devising screens other than with low numbers of individuals, kept this work as anecdotal stamp collecting (see e.g Hadorn, 1961). Nevertheless, it created a foundation for what was to come. In particular it provided a flavour for the kinds of mutants which could be found and, more significantly, for the fact that one could deal with SOME of these processes genetically. Classic mutants like bithorax and Krüppel in Drosophila, or T/Bra in the mouse, are a product of this period.

Wild type Drosophila larva (left) and mutant for wingless. From the Tübingen screens. On top how these mutants helped us understand the cellular basis of the cuticle pattern.

S. Brenner had been working with C. elegans along the lines that genetics would provide the answer to your favourite problem, whether it was how the nervous system was built or how it works but it was in the early 1980s that C. Nüsslein Volhard, E. Wieschaus and G. Jürgens carried out a seminal screen in Drosophila for embryonic lethal mutations. This work not only transformed developmental biology but laid down the logistics of these experiments and showed their potential as a deep tool of discovery (Nüsslein Volhard and Wieschaus, 1980; Nüsslein Volhard et al. 1984; Wieschaus et al, 1984; Jürgens et al. 1984). Screens had been done before, but except on very rare occasions, looking for visible viable phenotypes and, in the few cases of lethals, in much smaller scale. This was a large scale experiment (no free lunch here for anyone), organized with an almost military precision which yielded an embarrassment of riches that kept at least two generations of graduate students and postdocs working on its product. The screen was successful because the mutants it yielded were informative about biological processes. It was a high level screen; it selected lethal mutations and then looked at the phenotypes. Nothing more, nothing less. One of the most significant findings was that the mutations could be organized in classes which meant that there was a logic to the processes mediated by the gene products (Nüsslein-Volhard and Wieschaus, 1980). Of course, this had been seen before in bacterial research but here it was in relation to the making of an organism. The next few years confirmed this and, together with the molecular biology and related screens in C. elegans (see e.g Ferguson et al. 1987, Ferguson and Horvitz 1985) revealed that the components of the system and their function were evolutionarily conserved. This type of screen was extended and repeated to maternal loci and also to other organisms, in particular the zebra fish by C. Nüsslein Volhard herself with a large group of people, and much like in Drosophila, this screen (published in a special issue of Development in 1996) laid down the foundation of a field and generated work.

This is a good place to take stock. These screens worked well and the reason is that they were generic, that they looked at a process from a high level, that they asked very simple questions of how a process, a very general process as is the development of an organism, can go wrong. They provided information where there was ignorance.

Classes of screens

Broadly speaking there are three kinds of genetic screens: search for the effects of loss of function mutations and either suppressors or enhancers of other mutations. It is possible to present each of these in a variety of colours and flavours, which form the basis of the screen kit. The first kind (straight loss of function) is the one that was used in Drosophila, C elegans and A. thaliana in the 70s and the 80s and later zebra fish in the 80s and 90s, and requires large, but not impossibly large, numbers of individuals and a good logistics. Enhancers and suppressor screens are different. They start with a phenotype associated with a mutation and look for ways of either enhancing it (making it worst) or suppressing it (making it better). The little book “pushing flies” by Ralph Greenspan, explains much of this in simple and useful detail.

It should not come as a surprise that the first kind is easier than the second and that for enhancers screens to be useful, they have to be carefully thought out with a high degree of stringency. A very good example of an enhancer screen was carried out for sevenless in Drosophila, which yielded key elements of the Ras signalling pathway, thus revealing its linearity (Simon 1991); in this work sevenlesswas known to encode an RTK and using a temperature sensitive allele, the temperature of the incubators was exquisitely carefully set so that function was suboptimal but allowed for defects to be created by additional mutations in other proteins that interacted with Sevenless and decreased its function. Suppressor screens are more difficult to enact, but tend to yield riches, as one can be very stringent on the question (the screen) such that the answer, rare as it might be, would be informative (interpretation being an important element here).

Outline of a screen for alleles of wingless

As the events in suppressor screens are rare, they require large numbers (usually >106 or 107) which can only be afforded in prokaryotes, yeasts, some plants or, of the model organisms, only C. elegans e.g Sundaram and Greenwald (1993) –though they have also been performed in Drosophila (Karim et al. (1996) and Ferguson and Anderson (1992)) with good results i.e. they produced informative outcomes. Still, because the nature of mutations is stochastic and the events are independent, the numbers to be screened do not determine the actual success but rather its probability. Nonetheless, the crucial things of suppressor/enhancer screens are the numbers, their thresholds and, in the case of enhancers, a stringent second screen.

As genetic engineering has created new tools for the controlled expression of genes as well as different manners to follow expression at the level of gene or proteins, the possibilities of screens have increased. Nowadays the repertoire is often limited, only, by the imagination of the experimenter. It is also possible to screen whole genomes and with the advent of libraries of siRNAs or shRNAs and controlled overexpression, it is possible to generate screens of gain and loss of function,  of suppressors or enhancers, at will. More over, one does not need to rely on the organism to provide the phenotype as it is possible to engineer it by labelling organs, cells and/or proteins with tags, fluorescent or otherwise. And this is the tip of an iceberg. The possibilities are enormous and rising. The combination of these technologies with improved tissue culture methods have allowed to move into mammalian territories and to explore mammalian genomes in different cell lines, most significantly, in Embryonic Stem cells (see for example Guo et al. 2011 and Yang et al. 2012)

All in all, genetic screens have become the corner stone of all biological research and, more than metaphorically, the daily bread of the biologists ………..and counting.

The good, the bad of genetic screens……. What do screens really teach us?

Genetic screens were celebrated in a special collection of Nature Reviews Genetics between 2001 and 2003 (the art and design of genetic screens: http://www.nature.com/nrg/focus/screens/index.html). They are used world wide and taught in undergraduate and graduate courses as the way to gain knowledge in biological systems. There is a good justification for this in the successes of the past (see references above). However, like everything that is powerful (and genetic screens are powerful), all depends on how it is used; the topical gun in the hands of a child comes to mind. In the case of genetic screens, they work, they produce mutants and thereby information which needs interpretation. However, as we have been advancing in our knowledge and technical prowess, I surmise that we have not changed our ways, we continue to harvest mutants and, perhaps, it is a moment to ask questions: what do we get from genetic screens now? More to the point, do they make a difference, a significant difference, to our knowledge? I would argue that for the most part, they don’t any more, that at the moment we lack the framework and the knowledge to understand what they throw at us and that therefore in most cases, they provide elements of a curious collection of objects. Not always, not every screen, but most. Screens have become an easy road to a publication and all that this carries with it. Journals keep on publishing screens few of which are insightful. For the most part they end up, in the best of cases, doing little more than adding nodes to ever growing networks or providing new elements to processes for which we still do not have appropriate frameworks; rarely, do they yield something useful.

A good example of the good and the bad can be found comparing two published genetic screens in Drosophila geared to find the same things: genes that work with Notch (a classic gene encoding a single transmembrane receptor with important roles in development and disease). One of the manuscripts is sloppy, without a proper structure leading “to identify nuclear import pathways and the COP9 signallosome as Notch regulators” and concluding that “that complex developmental processes can be analysed on a genome-wide level” (Mummery-Widmer et al. 2009). Perhaps it will not surprise you that this was published in Nature and was hailed as an important achievement and a good piece of work; difficult to see the reason for this or the insight of the work. On the other hand there is a much more laboured and controlled screen targeting the same problem, which “revealed several modules of unexpected Notch regulatory activity. In particular, we note an intriguing relationship to pyruvate metabolism, which may be relevant to cancer”. Believe me, this one is good. It is sound, you get much of what you expect and more and all with proper controls (Sai et al. 2010). Whereas I would not put my money in the reproducibility of the first one I would happily bet for most of this one. It was published in Dev. Cell, though I know from the senior author, that this was not without aggravation and discussion (why do we have to always do this to publish in these journals?). The second screen is in vein of the 800,000+ flies of Karim et al (1996) with a similar slant, and is an example for whoever wants to undertake these experiments. But it is hard work, physical and intellectual.

Despite all the hard work, screens are about experimental design, organization and questions. There is no more to it. Most people can do them and, as I have said above, they pay: they do give mutants. The tragedy is that they are meant to help researchers and I bet you that many of them don’t. For the most part one ends up with situations like that of the Mummery-Widmer paper, many mutants but….how do we know if they are what we want.

The problem lies not so much in the screen itself, as in the need to think carefully about the question one asks beforehand, in the need of a good framework to evaluate the results, and in whether looking for elements of a complex system (and let us not fool ourselves, this is all screens will give you), whether this is the way to go about it. These days, genetic screens are used to probe into the workings of highly connected protein networks but rather than taking this into consideration, the designs consider linear relationships between the existing elements which they confirm with a crafty use of epistasis (see http://amapress.gen.cam.ac.uk/?p=914). The terms upstream and downstream are often used in these contexts and this regard. However, highly interconnected non linear molecular devices are difficult to break and much less when they are thought to be linear in the design. What sometimes happens is that, inadvertently, one does a screen in a particular cell type in which some of the feedbacks are disabled or the elements do not work well and then one gets an answer. There are too many tissue and sometimes species specific connections that can be misleading and the screen might reveal one of these in terms of a new element.

But the two biggest problems with screens today have to do with our lack of understanding of what I would call the ‘inner structure of biological systems” and how this affects the work.

The first one is that we do not look at what we should. At the helm of the cell is a set of proteins which we already know but whose workings (in the system sense) we do not understand. I am referring to systems like cell adhesion, traffic or signal transduction. The reason for a screen is often, always, to find a ‘new’ gene to then undertake a salesmanship job (if you think I am being cynical, think again on what you know). As indicated above, the best way to do this is with suppressor screens but even these sometimes might not work, so in most cases one sets up conventional loss of function screens that tend to be somewhat baroque. What happens then is a familiar story, half of which never sees the light of day. The one thing that most screens will do is to yield, in addition to mutants we have not seen before, mutations in genes and systems we already know; in particular in elements of Wnt and Ras signalling, cell adhesion and chromatin remodelling systems at the top of the list (and quickly behind elements of traffic and chromatin remodelling proteins). As this is not what we are looking for, we throw them away…….at our peril I would claim….and proceed to try to fix the ‘new’ things we have obtained and to connect them to some of the things/genes we already know. Genetics is sufficiently flexible to detect interactions which are usually good enough for an argument of relationship. We find our ‘pathway’ and presto, we can write a paper. As the point of the screen is to find new elements, so the point needs to be the ‘new’ things. The result is that we are left with a ‘new member’ of this or that pathway or a protein of unknown function which we hastily will find a way of linking to something we know. I am sure that if, instead of looking at the bright new things, we looked at what we know and asked why do we get this and not that, why X appears with Y in this screen and with Z in that other one? Why do we get this type of allele here and in some other screen we don’t? I bet you that if we were allowed to ask these questions, we would learn much more about the system than we do from the new genes which tend to be most of the time like characters in search of a plot.

The second reason why screens are problematic is that biological systems are highly redundant (in the sense of having multiple backups) and have evolved to respond genetically speaking, to selective pressures and a screen is, basically, a selective pressure. A biological system will always respond to the call of a screen by giving you mutants, even when we place the system in extreme situations. Take some of the screens in S. cerevisiae which, for example, making use of auxotrophic selection on Histidine, one can ask cells which lack crucial deletions of the HIS3 gene regulatory region which abolish the expression of the gene, to express the gene (Oettinger and Struhl, 1985). They do and (some of) the mutations turn out to be informative about the mechanism of transcription. This is dramatic, like resurrecting a dead individual. Similar experiments have been done  in E. coli, where the classical work of Barry Hall (Hall and Hartl, 1974; Warren, 1972) in which he asked E. coli lacking the ß-galactosidase gene to grow on lactose, set up a paradigm one should think about when doing genetic screens. In the experiment he found the mutagenic activation of another locus, call ebg, which can do the job of LacZ.

In many ways, either by mutation and selection or simply by selection, when challenged with a screen, the system will respond and will give you mutants. These are very extreme cases so it should not be a surprise that less stringent circumstances will yield more and more varied mutants. When a biological system is asked to give mutants, it does. In many ways that is what has been designed to do so as to respond to evolutionary pressures. Screens are doing only, what natural selection does: select and this will always happen.

So, one has to be very careful that when one sets a genetic screen one is asking a question about the process of interest and not asking the system how it adapts. We know that biological systems can adapt and no better example of this than what has been uncovered during the widespread use of siRNAs, RNAis and shRNAs: the immediate phenotype induced by these methods can be stronger and sometimes different than that of the genetic mutant. The reason is likely to have an element of the fact that the genetic mutant adapts and therefore, after a few generations, the organism (or the cell) has changed its phenotype (it needs to do this to survive). There is no clear proof of this, but it is all over the place and people have used this in their work (see Martello et al. 2011 for a good awareness of this). The degree of adaptation can be rather surprising and if you want an extreme case look at the work of Coudreuse and Nurse (2010) in which they can eliminate the mayor regulators of cell cycle progression in S. pombe and still achieve regulation through controlled expression of an engineered cycline dependent protein kinase (an imposed adaptation).

So, beware of asking questions about adaptation. One needs to learn not to ask a question about how the system can adapt to a situation but rather, how the system works. I would argue that the more we focus our questions, the more we are moving away from how the system works. And remember that Genetics will always, only, give you parts.

…and the ugly (or a swan in disguise?): The inner structure of biological systems

And thus to the end with what I would call “the inner structure of biological systems’, which is what consciously or (mostly) unconsciously we are probing in the genetic screens. It is early days, we are just beginning to get glimpses of this but the feeling one gets (and here I should say “I get”) is that the essence of this structure that we call a cell (and by extension a multicellular organism) is a collection of small networks, in the ‘alonesque’ (for Uri Alon) sense, each of which performs a logical operation (Alon 2007). These small networks are loosely connected amidst them (have discussed an early version of this in Trott et al. 2012) and the connections, which are really biochemical, fluctuate. There might be devices, molecular devices, whose function is to strengthen these connections in a cell type or situation specific manner, and I believe that Wnt signalling can be interpreted in this manner (Martinez Arias and Hayward 2006). These connections create an operational hierarchy with a lot of basic (in terms of the needs for the cell) but not regulatory stuff in the periphery, highly connected to the core (see below). The important aspect of such a structure is that it is reactive, that it can reorganize itself in response to its environment, and that it can adapt.

The early screens were unaware of this (if it exists). Unconsciously they targeted the key components of these networks, the hubs, and found that when mutating them many processes went wrong. This is what you expect from such screens because they look at and thereby select for those phenotypes. Having obtained the hubs and some of the networks as a result of these hits, we set up schemes to target the system in more fine manner and by doing this we turn our attention to the redundant networks in the periphery (without knowing and without knowing how they look which means that, often, we fail to understand). The new crop of screens is not very precise in terms of looking at the structure of the system, they are sophisticated but often all they ask is how the system rearranges itself in a stressful situation. The screens that work (i.e that provide information about the system) are those that target the structure and function of this core-networks, we could call them ur-networks.

Screens are expensive and time consuming and it is for this reason that we should think why do them and what we expect from them. Then target exactly that rather than embark in fishing expeditions for new genes, which will only add elements for a confusion. Most importantly, at this point in time before we collect more components we need a framework, or frameworks, of how the cell, its sensory system, that Dennis Bray would say, is organized and responds. We have to separate (and this is difficult) the actual working of the system from its adaptive nature…..but maybe this is not possible. But we need to try. One suspects that the outcomes of the screens are telling us something about the inner structure of the cell and we need to figure it out if we are going to make progress in our understanding of the function of biological systems. The ideas of Dennis Bray, clearly outlined in his book Wetware, are a very good reference in this undertaking.

An outline of what I mean by the ‘inner structure of biological systems’ will be published here shortly in the form of an Appendix to this commentary.

In summary

An understanding of the structure of the cell, physical and functional, will lead to new findings and the rational design of experiments, in particular screens. Most urgently, we need to figure out efficient ways to target connectivity in genetic screens rather than components, which is what is being done at the moment.


A biologist’s thought: Biology is indeed difficult……but rewarding when you understand something…..or you think you do.


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Stem Cells in Developmental Biology: a debate at the BSDB

Last week the BSDB (British Society for Developmental Biology) celebrated its annual gathering at Warwick. Always a good place to go for quality developmental biology which is enhanced by the arrangement of holding the meeting together with the BSCB (British Society for Cell Biology): these days there is much cell biology in developmental biology. One of the BSDB sessions focused on Stem Cells and highlighted the clear connection between this area of research and developmental biology, or so it seems to some of us but ……perhaps not all.

The AGM of the BSDB had, for the second year running, a ballot to change the name of the society to include “stem cells’ in its name. Thus, the proposal was to change the name from “British Society of Developmental Biology” to “British Society of Developmental and Stem Cell Biology”. The proposal had been flagged last year and, after a vigorous discussion, was rejected, but by a narrow margin which allowed the subject to be brought up again to the AGM this year, where it was resoundingly rejected. But read on……….

The discussion preceding the vote was heated and highlighted several misconceptions about research in stem cells which, perhaps, represent some reality.

The ones in favour argued, correctly I think (I was and am in favour of the change) that Stem Cell research is part of developmental biology and that while there is much that has to do with medicine, the links between Developmental and Stem Cell Biology are strong and essential for both fields, that Developmental Biology can bring rigour and direction to Stem Cell Biology and that Stem Cell Biology can bring challenges, new ways and possibilities for Developmental Biology. They (we) argued that, after all, Stem Cell biology has always been part of Developmental Biology, albeit somewhat cryptically. Including Stem Cells in the name of the society is an acknowledgement of the times and can have its benefits because there is no denying that Stem Cell Biology is a central and key element of research these days; including it explicitly in the Society’s agenda would allow the BSDB to have a strong voice in policy, funding and education in these increasingly influential area of research.

The ones against the change argued that Stem Cell Biology is different from Developmental Biology, that it has a clinical slant which would attract a different crowd to the meeting, force different content in sessions and, overall, distract us from the main business: the workings and evolution of embryos and systems. It was suggested that such a change would alienate several established constituencies within the society that would abandon the group. More significantly, that, eventually, with another vote a few years down the line, Developmental Biology would be booted out of the title for the society to become the British Society for Stem Cell Biology.

As far as a I am concerned this was a missed opportunity. While I appreciate many of the points made by the ‘noes’ , I feel that their arguments are based on fear for a future that will always take over no matter what we do and that, in the long term, there will be consequences from not seeing this. We live in an increasingly corporate world in which lobbies are important and, in the context of our business, provide the basis for funding and policy. For the Society of Developmental Biology Society to have an explicit voice in the Stem Cell community is not just an extension of its natural remit and interests, but it is a way to bring some real science into a field that is increasingly interested in applications without having covered the bases. The foundations of Stem Cell Biology lie in Developmental Biology and it is important that developmental biologists have a say on decision making in that important field. Stem Cell Biology is not exactly, as some people claim, a new area of research (developmental biologists have been working with stem cells and their lineages for years) but it is certainly an area that recently has come of age to carve its own intellectual niche like, in many ways, Developmental Biology did in the 1970s (let us not forget that Developmental Biology is an offshoot of Embryology). It was argued that Stem Cells are born with Till and McCulloch (1964 Proc Nat Acad Sci. 51, 29–36). True but what they were looking at is the question of the origin of the blood, a problem in Developmental Biology whether one likes it or not. At certain places, and stem cell research is one of them, boundaries blur. Is genomics and bioinformatics genetics? Yes it is. In my book, Stem Cell Biology is part, and a very important part of Developmental Biology.

But let us move away from the heart of the question (of course the scientific content) and look, briefly, to the context of the discussion. The boundary, as I have said is blurred, and a situation can develop (and in certain places is happening) that some people, funding bodies, society, come to see Developmental Biology through the eyes of an unbridled Stem Cell Biology. After all, is it not organs out of cells that is the goal of stem cell biology? And is it not understanding these processes the goal of Developmental Biology? Then, what is the difference? The answer is simple, Stem Cell Biology wants to do, Developmental Biology wants to understand. It would be a pity not to bring them together. One can see here history trying to repeat itself: throughout the XVIII and XIX century engineers and inventors were making steam engines with little knowledge of physics, and they worked, but it is when the knowledge of thermodynamics is brought into the framework of the engineers that the engines become efficient. The same can be said of computing where, again, it is physics that makes the hardware that we have today. The fundamental science will always help the more applied side and needs it. So, much to be gained from Developmental Biology having a say in Stem Cell Biology. But there is a second more difficult question: what will be the consequences of the agenda of stem cells running that of developmental biology?

I can see a marginalization of model organisms and a biasing of the agenda towards applied science, applied in a trial and error way, rather than in the tradition of Science. I might be wrong in the extreme formulation of these concerns but I am certain that some of this will happen.

In the end, my impression was that the ‘noes’ were afraid, afraid of the future without realizing that he future will happen and that by not seeing the trends and joining them, we shall always be left to mercy of those trends, without a voice to influence them. I worry that model systems that have taught us so much about basic biology will slowly be squeezed into corners because we do not have a voice to explain that flies have stem cells, that stem cells are part of the make up of an organism which cannot be understood outside its context, that stem cells are a problem of evolutionary biology, that stem cells are a linguistic twist of lineage analysis and lineage analysis has always been a problem of developmental biology, from Roux and Driesch to Garcia Bellido with Till and McCulloch in the middle. Incorporating Stem Cell Biology in the name of the society would have been a way of having a strong voice in a trend that is rapidly gaining momentum.

We shall see what the future harbours. The BSDB is a strong society which represents a vibrant and engaging community so there is no reason why things will change rapidly. However, one thing is clear: there is a need for the voice of developmental biologists to be heard in the Stem Cell community. A mechanism needs to be found for this. It is necessary as much to have a representation to remind that community where their real roots lie and the benefits of listening to the fundamentals of their field. There is a drift which was, unfortunately, at the heart of many of the speeches for the no, that Stem Cell Biology is more clinically than basic research orientated. One can see how this can be construed but, decisions like the one we have taken will increase this gap and foster this misunderstanding. It would be good (it is always good) to take lessons from history. As the interactions between physics and engineering prove, there is much to be gained from the interactions between a field that tries to find practical solutions and one that explain the causes of the problems. Let us hope that the BSDB can find a way to influence some of the directions of Stem Cell biology. For the moment it is as if two twins have been separated; each with their own mind but with shared genetics.

On epistasis, or how genetic analysis can mislead us about biological processes.

As I am about to embark on my brief lecturing stint in the department, thoughts about the subject matter come to mind. One that always concerns me is the value of epistasis (the exercise to create functional hierarchies of genes through the analysis of the phenotypes of double mutants) to learn about processes in developmental biology.

The problem is simple. Genetics is to Biology what mathematics is to Physics: a formal language that allows us to pose questions and find answers. A mutant screen is, in many ways, the formulation of a problem: what controls the decision of a bacterium to use glucose or galactose? What determines the polarity of an embryo? How does a cell orient iself in space? What we find is a collection of mutants which, through some use of our experience (and the rules of genetic analysis), we relate to particular genes. Today, thanks to advances in genomics and the accumulated knowledge of molecular biology, we learn quickly about the kind of proteins that the genes encode and we can weave one of those “Just so stories” that HIF (High Impact Factor) journals like so much: how the gene X affects the nose of the mouse, how the chicken got its wings, or how a neuron lost its way on the way to a muscle……in any event, an important element of the story is to weave the genes together into a “functional network”.  If the story is good it will be bought by a HIF journal and you will have a grant, a job, etc….Now, an important element of the story is the formulation o the relationship between the genes that relies on the analysis of double (and some times triple) mutants: epistasis.

When considering a regulatory process, epistasis allows us to create a linear chain of relationships between the elements (mutants) of the screen for pairwise interactions. The mechanics of epistasis is simple. It requires that the mutants under study (say A and B) have different phenotypes and then asks what is the phenotype of the double mutant (A, B). If the phenotype is B, this means that B is downstream of A i.e. A->B. If the phenotype is A, it is the other way around and A is downstream of B (B->A). If we now can do this with B and a new mutant C, we can construct an A->B->C chain and continue forward.

NB. This is fine in the abstract genetic world of phenotypes since, as those who grew up in metabolism know, when dealing with metabolic pathways, the reverse is true. Suppose you have two steps in which enzyme A catalyzes the change of X into Y, and then enzyme B catalyzes the change of Y into W; if A is mutant the reactions will accumulate Y and the action of B will be redundant i.e. in a metabolic pathway if the double mutant AB is A it means that B is downstream of A!!!! This difference highlights something interesting and perhaps deep about what it is that we measure with mutation; why the difference in this formal language between biochemistry and signalling? There are other uses of epistasis (see Phillips, P. (2008) Epistasis: the essential role of gene interactions in the structure and evolution of genetic systems. Nature Rev. Genet. 9, 855-867). 

Leaving aside terminological issues, there are several problems with the use of epistasis as a way to uncover the functional structure of a biological system, which should make us concerned. Here I would like to highlight three:

1. Machines do not have linear blueprints. The physiology of cells (and this broadly speaking encompasses the sum of the processes that allow them to survive, interact. process information and reproduce) is operated through molecular machines which are often multicomponent. What counts is the operation of these machines as wholes and this does not emerge from a functional linear arrangement of their component parts. I am sure that being clever one could make an epistasis of the ribosome; but this is nonsensical, as what matters is its function as one piece, not our interpretation of its function as the result of a nonexistent array of linear instructions.

2. Feedbacks create problems of interpretation. Feedbacks and time series, create loops in linear systems which can complicate the analysis of epistasis. For example, imagine a ligand X for a signalling pathway Y and a second ligand Z for a second pathway W. It could be that X activates Y which leads to the expression of Z and the activation of W. Epistasis would easily show that X/Y is upstream of Z/W but if now W activation leads to the expression of X (of course now X would act in a different context), we would have a problem for epistasis as X is both up and downstream of Z/W and the genetics could become very confusing. If to this scenario we add the possibility of a feedback of Z/W onto X/Y, the situation that we extract from the genetics would not be simple and certainly not informative.

3. Double mutants are misleading. The reason for this is simple, in a double mutant AB one is not removing two genes from one organism, but rather one is removing gene A from mutant B, or gene B from mutant A; and which one is not possible to gauge. The problem is that, independently of the system, what we are doing in a double mutant is to study the response of a new situation; the loss of B in an A mutant, or the loss of A in a B mutant i.e the reaction of an established and adapted genetic system (the single mutant), one we know little about, to the loss of a gene. This is an important point which deserves some consideration.

These are serious flaws in an analytical tool that is so widely used, and all of them need to be considered when interpreting genetic data. Single mutants are simple to read but even these, sometimes, can become obscure. What can be done?

There are no bad tools, there are bad uses of tools. You cannot cut steak with spoon, nor eat soup with a knife, at least not effectively. It is important to know the limitations of our tools and this is something we should do with epistasis. It can be useful and, indeed, sometimes double mutants are informative, particularly of one is close to a molecular understanding. For example, if a mutant for MAP Kinase is epistatic with a mutant for MEK (the MAP Kinase Kinase) or a Receptor Tyrosine Kinase Receptor (RTK) -in particular if these are activated- we can put our money that MAPK is downstream of both (and this is indeed the case), and built a pathway: RTK->MEK->MAPK which tells us something useful about the system. But, as in the case of the ribosome, there is little use in trying to work out a linear pathway in the dynamics of actin polymerization and we should think more carefully about double mutants.

Final comment: High throughput genetics has brought up a high throughput version of epistasis. Some studies have looked for synthetic lethal phenotypes which reveal that the % of lethal mutant phenotype is higher in double/synthetic mutants than in single mutants. About 16% of single mutants are lethal (Tong, A. H. Y. et al. 2004 Global mapping of the yeast genetic interaction network. Science 303, 808–813) whereas, surprisingly, example in a screen targeted to genes required for chromosome segregation, out of 230 interactions between otherwise viable mutants, 18% (42) were synthetic lethal (Measday et al. (2005) Systematic yeast synthetic lethal and synthetic dosage lethal screens identify genes required for chromosome segregation. Proc Nat Acad Sci 102, 13956-13961). Other studies have corroborated these figures and provide a basis to think about QTLs and human multigenic disease (see Phillips above for a discussion of these matters).

Epistasis is about interactions and, as what we want is to uncover function, we should be careful in the way we interpret them. Particularly in these screens, whether they tell us about the ways to break the system when it is weakened or whether they are telling us something about how the system works. My money would be on the first and on the message that this contains: biological systems are redundant, highly connected networks, with multiple backups (see for example Guet et al.  (2002) Combinatorial synthesis of genetic networks. Science 296, 1466-1470). Epistasis is a tool, and it needs to be complemented by many others when trying to infer the workings of the system. Some people call these secondary screens.