A new sort of engineering: II. Organizing self organization in Space and Time

Note: This is the second part of the last post and is not its final form. It will be updated and cleaned up in the New Year but wanted to share these thoughts with those of you who cared to read them before the treadmill catches up with me in the New Year.

 

The vis essentialis of Wolff, the Entelechia of Driesch, the new physical laws promised to Delbruck by Bohr, all found echoes in the famous book “What is life” by E. Schroedinger. This book, that meant so much to a few who went on to change Biology, deals with two questions concerning the physical nature of Life. The first one, central at the time, is the structure of the hereditary material. The second, more abstract and less emphasized in discussions of the book, focuses on the need to explore the thermodynamic basis of Living systems and in doing so it raises, again, the possibility that there might be new laws of Physics lurking in biological systems:

“Living matter, while not eluding the ‘laws of physics’ as established up to date, is likely to involve ‘other laws of physics’ hitherto unknown……. from all we have learnt about the structure of living matter, we must be prepared to find it working in a manner that cannot be reduced to the ordinary laws of physics. And that not on the grounds that there is any ‘new force’ or what not, directing the behaviour of the single atoms within a living organism, but because the construction is different from anything we have yet tested in the physical laboratory.

We must therefore not be discouraged by the difficulty of interpreting life by the ordinary laws of physics. For that is just what is to be expected from the knowledge we have gained of the structure of living matter. We must be prepared to find a new type of physical law prevailing in it”

By the time the book was written, the inevitability of Genetics as the key to unlock the chemical underpinning of living systems was widely accepted, and the double helix, the genetic code, the unravelling of the biochemistry of metabolism and the principles of gene regulation that followed, soon became the vindication of this statement. But, as Crick said, this was, and still is, all chemistry. New physical principles elude any questioning; perhaps, in the end, there are none.

A few weeks ago I attended a meeting of The Company of Biologists in Surrey (UK), “From stem cells to human development”. I went with a mixture of scepticism and curiosity. After all, how could one study human development? By studying I mean, not just describing it and comparing the normal with the pathological but rather doing the kind of work that, through the use of model organisms, has brought so much insight into the molecular and cellular mechanisms underlying the development of embryos. If we are just beginning to grasp how genes govern the development of mice and fish thanks to experimental intervention, how are we going to do the same with humans? It is not just that the material for these studies is difficult to obtain, it is that, with all reason, we need to be mindful of the ethics of this work. Such thoughts were in my mind fuelling low expectations. The meeting turned out to be, for me, a great surprise and the answer to many of my questions, I should have known, laid hidden in the title of workshop through stem cells to development”.

The meeting was a series of examples of what is becoming a clear fact to those in the know: cells are the vehicle between the genes and the organisms. Cells transform the instructions that lay dormant in the genome not just into proteins but into shapes and complex multicomponent forms. The structure of cells, and not just their physical organization but also their computational structure, drive their assembly in the macroscopic arrangements of different cells that we call tissues and organs, and this manifests itself, more than anywhere else, in the surprising self organizing activity of stem cells, embryonic and adult. Take cells with the right potential, place them in the appropriate culture conditions, ignite them with a signal and a genetically driven process will be unleashed that will transform a sequence of nucleotides into a multicellular structure. And the meeting showed us how human eyes, neocortexes, intestines, lungs and blood, emerged from stem cells, embryonic stem (ES) cells. Watching these unfold it is difficult not to think of these processes as manifestations of the vis essentialis and see in these cultures the opportunity to tackle its physical, or if you want to be more conservative, physical-chemical nature. And it is in watching these wondrous processes that the possibility of novel physical principles lurks again in the background.

The notion that cells derived from embryos have a self organizing activity had been known, but perhaps not appreciated, for some time. Thus, Holtfreter and Barth (discussed in a modern light by Hurtado and de Robertis 2007 Dev Biol. 307, 282-289) had observed that animal cap cells from Ambystoma maculatum salamanders, will differentiate autonomously into structures which resemble anterior cortex and develop eyes in culture. Furthermore, attempts to understand limb development and patterning contain numerous reports of mesenchymal cells, jumbled up and wrapped in ectodermal coats, generating digit like structures with recognizable identities. In the premolecular era, this type of experiment was the bread and butter of the experimental embryologist but though guiding much developmental biology, at the time there was little chance of understanding them. Over the last twenty years the application of the methods of classical genetics to development and pattern formation have yielded a catalogue of genes associated with particular processes. In this endeavour you remove a gene, look at the consequences for the organism and then try to work out what was the job of the gene in the process that has gone awry. Connections between genes are worked out through the process of epistasis. While this works very well with linear systems and particularly with metabolic routes, things can get out of hand with complex processes involving non linear systems like cellular machines, or processes like most of development and pattern formation. In particular, it is possible to find molecules that will induce nervous system from ectoderm or digits out of mesenchyme but, what about the process itself? But there is more to a process than its outcome; in fact the process is more interesting than the outcome. Is there a way to tackle its dynamics (the vis essentialis), the way cells proportion tissues and organs (entelechia)? Here perhaps, one needs to take a page (or a piece of the blackboard) of Richard Feynman who famously said: “that which I cannot build I do not understand”. This has been taken much at heart by synthetic biologists who ever since the ‘repressilator” (Elowitz, M. and Leibler, S. A synthetic oscillatory network of transcriptional regulators. Nature. 2000 Jan 20;403(6767):335-8) have been testing the information processing capacity of genetic circuits. But, in terms of Development, we are very far from being able to synthesize the very complex circuits and networks that drive the emergence of organs and tissues. Enter the cell.

Over the last five years there have been an increasing number of reports highlighting the ‘self organizing’ activities of cellular ensembles derived from stem cells. In work pioneered with intestinal stem cells, two cells from adult intestines can give rise in culture to structures that resemble very much in terms of composition and organization, the villi that configure the mammalian intestine. The same has now been shown to be true for other tissues, including lung and liver. However, in an extreme version of these experiments, the late Y Sasai (De Robertis EM. Yoshiki Sasai 1962-2014. Cell. 2014 Sep 11;158(6):1233-5) and his colleagues were able to, under specific culture conditions, coax ES cells to develop into retinas and neocortex. What is more, if the ES cells were from mouse, the emerging structures were sized as in a mouse but, if the starting point were human ES cells, the end point has the size of a human retina (Sasai Y, Eiraku M, Suga H. In vitro organogenesis in three dimensions: self-organising stem cells. Development. 2012 Nov;139(22):4111-21. doi: 10.1242/dev.079590). What else do you need to think about a driving force that is tailored to a particular species and which is able to asses in such a precise manner its final size and proportions? The meeting in Surrey had its share of these phenomena: human ES cells proliferating and turning into intestines, lungs and blood, which highlighted the cells as the architects of the organism through the interpretation of genetic programmes. But how do we get at the physical basis of these structures? Are there any new principles or physical laws behind these observations?

I do not think that self organization is the right notion for what is happening in these experiments; in some way what these cells do is, principally and certainly initially, to organize; however, as it is likely that everybody understands the term self organization, I shall stick to it – though in places I would rather remove the self: the ensemble self organizes, a cell organizes. In this context, there is something important, perhaps fundamental, we do not yet grasp –and need to come to terms with- in the fact that it has to be stem cells that do this and that their label of origin determines the final structure. The most straightforward interpretation would be that what stem cells can do and do remains deeply buried in their genetic programmes and that this is what fuels their organizing potential. Experiments in Drosophila shed some light on this. The Eyeless gene is at the top of a genetic hierarchy which controls the development of an eye. Eyeless is conserved in vertebrates, Pax6, in terms of structure and function -though Pax is involved in several functions, it is also involved in several aspects of eye development. Surprisingly, expression of Eyeless in any cell of the developing fruit fly will lead to a compound eye and, in this context, Pax6 will do the same thing. The simplest explanation for this is that Eyeless drives a deterministic programme for eye. Pax6 will do pretty much the same thing i.e. if expressed in Drosophila it will do the same as Eyeless. What this must mean is that Eyeless and Pax6, which are transcription factors, elicit a programme which in Drosophila’s software will produce a compound eye, the eye of Drosophila. There ought to be a homologous programme in vertebrates as Pax6 is required for the development of the eye. This is not self organization, but highlights that once a programme is initiated in a cell or a group of cells, it will be followed to term. It is maybe that some of what is going on in the cultures of stem cells have a component of this: a programme gets activated which in a deterministic manner will lead to the particular structure. The self organizing component comes into the picture the minute that there are different cells in the culture which now will not lose their way and will assemble themselves into specific structures. It is interesting and ill understood that this organization requires a 3D organization. However, it is important to realize that in this self organizing potential and much of what we can do is to steer this potential with alchemic precision. However as Jeremy Gunawardena once pointed out to me, there is hope since Chemistry is Alchemy with numbers!

Many questions emerge from these observations as well as many experimental possibilities but, new physical laws? New physical principles? Unlikely. Nonetheless and without getting too philosophical, there are two issues where Biology and Physics meet in these experiments which might lead to new notions or conceptual frameworks about the nature of space and time, what I would call the nature of biological space and time. Enough space left to just outline these and, paraphrasing Fermat’s margin, state that there is much to discuss on this, but not enough room here (or patience left in the reader) so, I will just make a few statements. The experiments with stem cells provide a system to determine how cells measure space i.e why mouse and human ES cells will each produce structures with sizes appropriate to their genetic blueprints? Where is this encoded? How is it decoded and executed? How do adult stem cells keep homeostasis of the size and shape of tissues? How do cells create such defined forms and shapes with a high degree of reproducibility? In an interesting observation, aggregates of ES cells have a critical mass to develop into specific patterns: above it, chaos; below it, inactivity. How do they know? How do they sense? But in addition to Space, there is also Time. And it is in this notion that new concepts, perhaps principles, will emerge. Time is central to biological systems as their dymamics, at any scale, is a most intrinsic property. Time, as is well known to physicists, is the most subjective of variables (as the physicist Sean Carroll puts it paraphrasing St Augustine : “I know what time is until you ask me for a definition about it, and then I can’t give it to you.”) however, biological time is not related in any simple manner to astronomical or sidereal time and when we do make this correlation we might be making a mistake. Take the process of somitogenesis (somites are the building blocks of vertebrates} which is run by a molecular oscillator whose elements are conserved across species but whose period is different in different embryos. But this difference is in astronomical time, perhaps from the perspective of the ‘system’ it does not matter, they are the same. How should we think about this? We can see these transformations in many processes which are run by the same molecular networks but take different astronomical times in different organisms. Is there a difference between the time of the networks and astronomical time? Time, as measured by the activity of genetic circuits (a network is not a circuit), is important for the correct decoding of ‘morphogen gradients” and is probably encoded and created by the activity of those circuits. If there is a process in which time is central it is gastrulation in birds and mammals. Furthermore, here, the convergence of space and time is the essence of the process. In these embryos, gastrulation is associated with a structure called the Primitive Streak: cells get progressively drawn into a groove through which they transit to generate the primordial of the different organs. There is an order: extraembryonic, blood, endoderm, heart, somatic…..what determines what a cell does is not its position in the embryo but the time and the order at which it enters the streak. There is a temporal programme which must be written in the gene networks and the circuits they produce. As JA Wheeler said, “time is the way to ensure that things do not happen all at once”. Nowhere is this more clearly stated than in many biological processes and most and best of all in the process of gastrulation in birds and mammals. It is in understanding how genetic circuits generate and interpret time that many new insights will come about in biology and how we might find some novel physical notions (and its relationship to space). It is also likely that this is the vis essentialis and Entelechia.

There is a tinge of engineering in the way we are handling ES cells, but of XVIII and XIX century engineering in the sense that we are tinkering with something we do not quite understand and somehow getting it to work. However, unlike mechanical, civil or chemical engineering where humans run the system, in this engineering of cellular organization, the system rules and runs the scientists, using a blueprint that, for the time being remains hidden in the deep cellars of the cells –to emphasize that we really do not know where it lies.

Interesting and exciting times ahead as accessing that blueprint will reveal new principles and mechanisms, if not physical, certainly biological. Not just the notion of how cells generate time, their time, but also the averaging of fluctuations at any level at the higher level of organization e.g molecular to cellular, cellular to tissue. A new kind of engineering indeed.

 

A new sort of engineering: I. Of inner forces, programmes and duality in living systems

Biology is a young science and this is easy to forget. For all the hype and glamour of modern conferences and publications, we still are in the midst of empirical data gathering. A bit what astronomers and tinkerers were doing in the XVII century. We have changed collecting and classifying beetles and butterflies for genes and regulatory regions, but the method has not changed that much: systematics.

This aside, there are, let us say, three issue in Biology: how a system builds itself, how it works and how it evolves, We know a lot about the second, have a good hypothesis about the last one and think we know, though really we do not understand much, about the first one. Our knowledge about the functioning of biological systems is reflected in the way we use this knowledge in immunology, cancer biology and neurobiology. However, this praxis is a bit like the building of devices by engineers in the XVIII and XIX centuries, empirical, and it will improve once we understand the underpinning of the systems. In Biology this means to understand the connection between genotype and phenotype, how genes build organisms, which we don’t. If we agree (and you don’t really have to) that this is THE problem, you will see that something is changing though, and the roots of this change can be found in history. When something repeats itself in history it is that it has some deep roots and we should not ignore it. The seeds of the story I want to tell lie with C.F. Wolff , follow with H Driesch and reveal how for a while, perhaps necessarily, we had to forget the important questions, though we don’t have to any more. Wolff and Driesch saw the questions and those questions are, today, at the forefront of the agenda of biological research.

On forces: CF. Wolff and H. Driesch

Slide4

In the midst of the XVIII century, guided by a curiosity about the development of embryos, C. F. Wolff carried out a number of dissections and reported findings that challenged the well established theory about the emergence of a living system; preformationism. The leader of this view was A. von Haller and Wolff entered into a lengthy and hard, though always polite, diatribe with him (for details see S Roe). In contrast with the at the time prevalent view that the embryo was preformed but not visible, Wolff favoured the notion that the organism emerged progressively from an informed mass which acquired shape and form progressively. The preformationist view may seem silly from the perspective of today but, it is not in the historical context, and I suspect that we also harbour many ideas that will look silly from the perspective of the future; the ‘power of the gene’ being a most interesting one. Wolff’s view was called epigenesis and its contrast with preformationism, took years to develop –such things always do-. Nonetheless, Wolff made his point and described how organs appear progressively from amorphous masses of tissue (cells were not yet the units of development), in two treatises (“Theoria Generationis” and “De Formatione Intestinorum”) and most clearly in the second. One question that Wolff was interested in was, naturally, what propelled this epigenesis.

Now, Physics had a good grip of human reasoning at the time. Since the time of Leibniz, natural philosophers (aka scientists) were aware of the existence of vis or forces and, in particular of a vis viva, which drove the motion of bodies and later became known as kinetic energy. What Wolff had described led him to speculate on the existence of a vis (force) of sorts driving the emergence of shape and form; he called this force ‘vis essentialis’, a formative force or energy. The notion has often been hijacked by vitalists but, if you thought about it, ‘vis essentialis’ is not, like potential energy was, some spooky spiritual notion but something which tried to account for some observations. Reams of philosophy have been written on vitalist interpretations of the vis essentialis but let us not digress from the simple point that Wolff had identified some internal inertia of a biological system that was precise and reproducible and which he claimed had a physical basis. History and some historians have a habit  of making a meal of what someone may or may not have said or thought but the fact is that Wolff only tried to encompass with words what his intuition told him lied behind what his eyes saw. The thought was laid to rest while the dust settled in the epigenesist/preformationism debate which would be won, as we now know, by force of observation on the side of epigenesis.

Slide1 

The XVIII and in particular the XIX century are rich in the description of the development of all sorts of organism and this descriptive phase takes over until towards the end W Roux in his very programmatic statements opening the journal that bears his name (“W Roux Archives of developmental biology”, nowadays “Development, genes and evolution“) ushers developmental biology as an experimental science, away from the mire of descriptive embryology.  It is in this context that H Driesch makes his formidable entrance into the story with a series of experiments which, unknowingly, set up the agenda of developmental biology for the XX century. In the first and most famous of experiments he separates the first two blastomeres of a sea urchin embryo which, under normal conditions each would have given rise to a half of the organism, and watches what happens. As he puts it in his famous paper: (Driesch, H. 1892 Zeitshrift für wissenshaftliche Zoologie 53, 160-178 Translated to English in Foundations of Experimental Embryology 1964 B. Willier and JM Oppenheimer eds Hafner Press)

“I awaited in excitement the picture which was to present itself in my dishes the next day. I must confess that the idea of a free swimming hemisphere or a half gastrula with its archenteron open lengthwise seemed rather extraordinary. I thought the formation would probably die. Instead the next morning I found in their respective dishes typical, actively swimming larvae of half the size”

Leaving aside the style (what a wonderful time when you were allowed to muse over your results with freedom!), there is nowhere to hide the result which contradicted a view, descended from preformationism and prevalent at the time, that embryos are mosaic…. But the result is surprising, the cells regulate, each gives rise to a whole organism. He repeats the experiment at the four cell stage and later in a series of variations, and finds very similar results. He ponders how can this be.

 Slide2

In 1911 he gave the Gifford lectures in Aberdeen where he looks back at his work. The book that comes from the lectures is, for the most part, an apology of vitalism. After all, Driesch did become an unrepentant vitalist in the second phase of his career, but the first part of the book is an excellent summary of his toilings with the experimental observations that led him to ‘despair’; in a mild manner. The section concerning his reasoning through his experiments in an attempt to find a rational explanation for what he was seeing, is remarkable reading and I suggest you look at it (see here some of it). An important point in this text is where he tries to reason what kind of a machine could behave like this and he reasons.

Much as Wolff earlier, he lived in a physics led intellectual environment in which engineering and machines were part of the daily life. More than Wolff, he lived in the hayday of engineering and machines. One guesses that both Physics and Engineering provide a guide to think rationally about the seemingly irrational principles that guide living systems. So, what he wondered in a mechanical analogy is whether one could describe a living system as a machine and if so and in the light of his experiments, what kind of a machine should this be. In his own words:

We shall understand the word ” machine ‘ in a most general sense. A machine is a typical configuration of physical and of chemical constituents, by the acting of which a typical effect is attained. We, in fact, lay much stress upon embracing in our definition of a machine the existence of chemical constituents also; we therefore understand by the word ” machine ” a configuration of a much higher degree of complication than for instance a steam-engine is.  (….). And we know, further, that this truly whole development sets in irrespective of the amount and direction of the separation. Let us first consider the second of these points. There may be a whole development out of each portion of the system ” above certain limits ” which is, say, of the volume V. Good! Then there ought to exist a machine, like that which exists in the whole undisturbed system, in this portion V also, only of smaller dimensions; but it also ought to exist in the portion V^ which is equal to V in amount, and also in V2, in V3, V4 and so on.

Indeed, there do exist almost indefinitely many Vn, all of which can perform the whole morphogenesis, and all of which therefore ought to possess the machine.(…). A very strange sort of machine indeed, which is the same in all its parts (Fig. 14) ! But we have forgotten, I see, that in our operation the absolute amount of substance taken away from the system was also left to our choice.

 From this feature it follows that not only all the different Vn, all of the same size, must possess the hypothetic machine in its completeness, but that all amounts of the values  Vn – n, n being variable, must possess the totality of the machine also: and all values Vn – n, with their variable n, may again overlap each other. Here we are led to real absurdities !

He is absolutely right, what he is describing is, basically, a cell but, of course, at the time, cell biology is prehistoric, genetics does not exist and the functional structure of a cell is not even on the cards. So, he exclaims with despair “….no kind of causality based upon constellations of single physical and chemical acts can account for organic individual development; this development is not to be explained by any hypothesis of configuration of physical and chemical elements”. And,slowly, he turns towards vitalism for an answer. But before, just before, he leaves us a gem of his understanding of what needs to be explained. In trying to understand the development of an organism, he suggests that there must be a function of different variables that decides what we would call today the fate of a cell in development

pv (x) = f(x, l, E)

Where pv(x) is the prospective value of element x (which we could see as a cell), s is the absolute size of the system, l is the position of element x and E, the most interesting of all variables, is the prospective potency, what he called Entelechia. This notion had been used by Aristotle and Leibniz, but it is with Driesch that it lives up to its own etymology: Entelechia means ‘that which bears its end within itself’, and it is not difficult to see a connection between the vis essentialis of Wolff and the Entelechia of Driesch. Both are trying to grasp the observation (or intuition if you wished) of some internal material or measurable inertia that is reproducible and drives the generation of form in living systems. Unknowingly this is addressing the issue of the genetic programmes that drive development and that today we can see as the basis of both interchangeable notions. A. Garcia Bellido has been a modern bearer of these notions and the one who has placed Entelechia on a genetic footing, one where we can begin to try to think about the genetic programmes that drives the system (Wolff) and the system that drives its homeostasis (Driesch), developmental and adult.

More of this next time but before that, to wrap up this historical background a brief account of the last pre-genetics/cell biology ditch to search for a physical explanation of Biology.

On duality: N. Bohr and M. Delbruck in Copenhagen

Slide3

In 1932 Max Delbruck arrived to Copenhagen to meet the members of the famed School of Copenhagen of quantum mechanics. The day he arrived, Bohr was giving a lecture entitled “Life and light” in which he would tackle the problem of the physical nature of the phenomenon of Life. This was taking place at the height of the development of Quantum Mechanics and the wave-particle duality exhibited by matter and light had been accepted, understood and interpreted. In his lecture, Bohr speculated that maybe there was a similar duality for Life, and that in this case, understanding would emerge from probing this dual nature which, in his opinion, would have a material and a vital element. In this context Bohr wondered whether the study of Life might not reveal new Physical principles, much as the deep study of matter and light had revealed to Physics at the beginning of the century. Life was, after all a physical phenomenon. Delbruck was in the audience and was very taken with this lecture; with encouragement from Bohr and Heisenberg, he turned his attention to Biology. Intriguingly, although he founded the Phage School which led to molecular Biology, he never found the new laws of Physics in Biology, that Bohr had made him think about in Copenhagen, though he continued to search for them all his life.

Almost a century later, Life, Biology, has not produced many dramatic new physical principles, certainly not in the physical sciences. Crick provides a reason for this state of affairs when he contrasts Delbruck, searching new laws of Physics, with Pauling on the trail that Life is just chemistry. As he puts it “so far history has proven that Pauling was right”. For the moment the triumph of Chemistry is clear: life is just chemistry in nonequilibrium conditions and Biology has not needed of any new physical concept in its main body of knowledge. However, Crick made the proviso of ‘so far’ and we might be on the verge of some surprises which could explain what Wolff and Driesch sensed in embryos and Delbruck searched in vain: the inner forces that shape embryos and endow them with the ability to control space and time (next: A new sort of engineering II. Genes, time and space. Supervising self organization ).

New publication on “symmetry breaking in ensembles of ES cells”

figure-01

The left picture is a group of ES cells bearing a reporter for Wnt signalling (red) in adherent culture, the middle one is the same cells in an elongating ‘organoid” which we call a ‘gastruloid” -notice the localize expression of the reporter-; finally the picture on the right is an embryo bearing the Wnt reporter at a stage we reckon mimics that of the aggregates in the middle. Picture on the right courtesy of Christoph Budjan.

New publication on “symmetry breaking in ensembles of ES cells”

Progress on our attempts to understand the connection between genes, signals, cells and embryos have just been published in Development. In a first paper we describe a new experimental system in which we coax mouse Embryonic Stem cells to make structures with an anterior posterior axis and a germ layer organization that resembles that of an embryo (http://dev.biologists.org/content/141/22/4231.full). In a second paper we use this experimental system to gain some insights into the emergence of the spinal cord (http://dev.biologists.org/content/141/22/4243.full).

You can see a movie and some thoughts on the experiments here: http://www.cam.ac.uk/research/news/shaping-up-researchers-reconstruct-early-stages-of-embryo-development

More on this will follow soon.

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/

Summer Musing

What is your favourite experiment? This is a question that is bound to come up in conversations of scientists, class rooms or retreats. It is sort of like: what’s your favourite novel or your favourite painter. It is always difficult to answer because one is bound to be wrong with what it is said on the spur of  the moment. Whatever one  says –and you will know if you have been here- you will change your mind later, because what you have said is what you remembered. Given time you are likely to come up with a list of experiments (or novels, or painters or pieces of music) which would be difficult to tease apart. In the end, logic and emotion will collude to choose a favourite. So, the other day I asked myself: what is my favourite experiment?

As a biologist there is no shortage to choose from. Some of the best and most popular ones come to mind. Avery, MacLeod and McCarty showing that DNA contains the hereditary material, Pasteur’s removing once and for all the notion of spontaneous generation. Of course, Meselson and Stahl’s beautiful proof of semiconservative replication. There is not much to match any of these in the last twenty years, largely because in Biology we have substituted Science for data collecting and gene (I mean bean) counting (something the big journals love). In the physical sciences there are many exceptionally beautiful experiments: the double prism experiment of Newton, the measurement of the bending of light by Eddington, the weighing of Oxygen by Lavoisier……. the list could be long; all tributes to the ingenuity and beauty of the human mind.

As a developmental biologist I have always been seduced by the experiments of Driesch in which he separated the two blastomeres of a sea urchin embryo only to find out that they would form two embryos, rather than two half embryos. And of course, the epic cloning experimentss of John Gurdon, which have an interesting history. These experiments are characterized by their conceptual simplicity but technical challenge to answer an important question.

But when I think about it, my favourite experiment is one that I rarely hear mentioned in this light. It is simple, even boring, but somehow ever since I heard about  it, has captured my imagination. It was performed by R Boyle in 1662 and, as I recently discovered, had the assistance of R Hooke in its design. Boyle had been interested in what he called “the spring in the air’ which led him to what we know as Boyle’s law, namely that Pressure is the inverse of Volume in a gas. While on this subject he had the idea that sound required the deformation of air i.e. that it was a form of pressure in the air. To prove this he prepared a remarkable contraption which allowed a bell to be placed inside a container from which the air could be removed –at the time methods to create vacuum efficiently had been discovered-. Now, he and his friend Hooke figured out a way to manipulate the bell inside the container as the air was being extracted .And herein the beauty of the art. The bell is moved before pumping out the air and it rings, then as the air is drawn out, the sound is dampened until, vacuum created, bell dangled, no sound! QED beautiful, simple, impactful. I can imagine the audience, dumbfounded.

No rational for this choice, many of the others (and many more that you can think of) will do just as well. I guess, all down to the fact that one of the beauties of Science is the sense of awe and wonder and this experiment has a good dose of both. It is also that thinking about experiments like Boyle’s and the others should serve as an inspiration and push us to think about good questions and good experiments to reveal the inner workings of Nature. This is the way it used to be and where we need to return.

Publish: What? Why? Where? How? – Part II: Solutions?

These are notes for a lecture given by AMA in a workshop about Responsible Research held at LMU in Munich (Germany) on 24 July 2014 (www.responsibleresearch.graduatecenter.uni-muenchen.de/index.html). The lecture is broken into two parts, the first one dealt with biomedical publishing, its origins and current state. This is the second instalment on solutions. Videos of both the lecture and the subsequent panel discussion are available at www.responsibleresearch.graduatecenter.uni-muenchen.de/presentations/videos/index.php 

The problem is, to a certain degree, clear. Let me recap. What was conceived as a way to communicate between scientists and between scientists and the public has become a measure of success, a ruler of quality and an arbiter of professional development. The change in character has altered what science is, how it is done and how scientists are evaluated; too many papers, difficulty of separating the wheat from the chaff, limited funds….Nowadays to do good science is not good enough. To survive in science one needs skills like being able to ‘sell’, being a good story teller, being able to chat up editors, being savvy on more than the subject matter, and then combine these skills to get money. Furthermore an increasing blur between data and thought, between science and accounting creates a climate of confusion in which money talks. Spin and good PR are as important as deep science and enquiry. And an important reason for this is that what we are working with is a XIX century system that has never adapted to the times. What we have, as I have said before is a collection of XVII century tulip bubbles about to burst –the glamour journals- sustained by a few. But there is change coming (I think) and we need to support it and make it grow. Here are what in my view are the important elements that are leading this change

First, Open Access. This is a most important development and one that for the most part has achieved its goals. You have heard a great deal about this so I shall not dwell on it. Open access is a natural response to the attempt of several publishers to own your/our work, to the fact that science has become a business for the journals but it is our toilings that they work with. Open access is not free publishing but it is rational and sensible publishing and it is good to see that funders of science have rallied to support this move. Everybody should publish Open Acess. While everything is good here, we should not lose sight of the fact that the big publishers have seen the goose of the golden eggs and have rallied to produce their own Open Access journals that take advantage of their brand names to make more money. And this takes me to the next all important issue New Journals

Partly because of the publishing niche opened up by Open Access, partly because of the increasing demand for space to publish driven by an exponentially increasing output, new journals emerge every month. Do we need them? How do we decide where to publish? Are these journals changing anything or are they mere derivatives of what we already know? The latter is often the case and clothed with the mantle of Open Acess there is a barrage of faked and real journals which tempt us with more or less success.

There are however positive exceptions which are actually trying to move away from traditional models and aims. At the forefront is a new journal called eLIfe; you have heard about it earlier today. It is an online only journal with much to be commended for. I am particular fond of their reviewing procedure and many technical aspects of how papers are presented, the kind of discussions it posits and the support it has from three heavy weights of research funding (Wellcome, Max Planck and HHMI) which makes it a statement of intent. It is a scientists journal which is trying to carve the future. But…….they have a problem, namely that the people who run the journal are the same people that brought us Cell, the rightly maligned impact factor, who review and publish in Nature, Cell and Science and who control where you publish, how you publish and whether you get a grant or not. How can you implement change with the people who created, and still favour, what you want to change? I guess the answer is with difficulty. Furthermore, they promote openness and yet, many letters of rejection are signed by their chief scientific editor, Randy Shekman, independently of the field, because the editors in charge want to remain anonymous. This is not a good advertisement, But remember what I told you, most of the people behind the journal are the same ones who have created the problem that eLife claims to want to solve. So, while I applaud what they want to do, they still have work to do. Also, the stated aim of the journal is to compete with the glamour journals, but to do so in a fair manner, by attracting quality. But here we hit another problem and this is the difference between quality and cool and eLife, inevitably, is so far a mixture of the two with a heavy dose of cool. But I do not want to knock them down because they have much riding for themselves and have an opportunity to do something transformative and help us move forward. Take these comments as a recognition of their toilings and their openness to new ideas. They can succeed but they need to be bold, really bold and not fall sleep in their coolness. And it is for us to make sure that they deliver.

I mention eLife because it is, in my mind, the most interesting project but do not forget others. Most interesting amidst these, the loved and hated PLoS ONE which, as anybody who has published in it knows, is not just a place where you pay and publish (there are many of those). It is a serious journal in the spirit of publishing sound, rather than soundbite, science (notice the irony! I have often heard as a criticism of PLoS ONE that it ONLY wants to publish sound science……….). Sure it is a mixed pot but I have never had a paper published there without proper revision and their acceptance rate is around 70%. It is a pioneer. Other journals have emerged as derivatives of mainstream products and thus the Company of Biologists have Biology Open and Nature and Cell Press continue to expand their portfolio to fill their pockets with Open Access journals. So, the choice today is very large. My advice here is simple: publish where you feel it is more appropriate. Do not waste your time in the lengthy and morale-sapping process of peer review in the glamour journals. It is not worth it and certainly not worth your time. And yes, wherever possible use scientist based journals.

Untitled.1-002One interesting development in terms of ‘new publications’ is the emergence of preprint servers. This is a notion that comes from the physicists’ arxiv (http://uk.arxiv.org/), which has been running successfully for over twenty years (founded in 1991). In fact arxiv represents the main avenue for publication of new findings for the physics community and they do not worry too much about impact (the biosciences flavour); what they worry about is precedence and being read and discussed. How does it work? When you have results that amount to a manuscript, you prepare them and post in arxiv; you get a doi and you wait for comments or simply mature the work (you can upload new versions of the manuscript). In the meantime people can see the paper. Then when you think it is ready for ‘official’ peer review, you submit it to a journal, and most journals, including Nature and Science, accept papers that have been posted in arxiv (http://en.wikipedia.org /wiki/List_of_academic_ journals_by_preprint_policy). There are good reasons for this: Nature and Science are journals where physicists publish, as arxiv is a central element of communication for the physics community, Nature et al have to accept the rules of their game. A lesson here: Nature and Science have to accept the rules of the scientists and notice that Cell press does not like arxiv. There must be a good reason for this: it is a publication. Over the last few years, biologists with a more quantitative inkling have begun to use arxiv, and this has led to a new section in the journal on quantitative biology. As a response to this interest of biologists in using arxiv, and as a way to rally the more traditional biology community, a few months ago BioRxiv (http://biorxiv.org/) was launched, a biological version of arxiv. It is working well, has not yet gathered momentum, but it hails a cultural change and I very much encourage you to use both arxiv and bioRxiv. There are other preprint servers, as they are called e.g PeerJ, Figshare and F1000. So, again, you have a choice.

Untitled.3-001Why use Preprint servers? There are many reasons and I have discussed the matter before ((http://amapress.gen.cam.ac.uk/?p=1239) but here you have two which should be of interest to you. One, because it gives your research quick visibility and establishes precedence. Two, because it gives you a doi and with it, the ability to refer to it in applications and also in papers. As I say, this is the bread and butter of the physics community and I do not understand why it should not become ours.

And publication rolls on to the next topic, an all important modern classic, Peer review, which echoes much of what I have said in the first part, so I shall be brief. Few people would disagree that peer review in the biomedical sciences is in crisis and changing it should be the next target of our community after Open Access,. Peer review is not doing the job that it is supposed to do. At the moment, the main role of peer review is to make it difficult for you to publish and the degree of difficulty is proportional to the perceived glamour of the journal and, in the journals where this index is high, inversely proportional to your interactions with editors and members of the editorial board. Remember the remarkable advice from the Cell Press editor I mentioned earlier. Anybody who believes that peer review does a good job is dreaming. Please do not think that I do not want peer review. Nothing further from the truth but, I do not want a surrealistic process which has so much element of chance and cliquishness.

There are no easy fixes here. The peer review is the community. We do need peer revew, but we need a system which avoids the extended essays and legal arguments which bedevil the system at the moment. The longer you are in this business, the less you trust the system. These days the collection of reviewer’s comments and replies can be longer than the paper itself! Some journals, like EMBO J and eLife have interesting leads that should become common practice: one, and only one, round of review (both of them and extending) and, in the case of eLife, comments reduced to 500 words (one page, if you want to be generous). There is no reason why one needs more space to assess a paper. A review is not about the paper the reviewer would like to write with the data and resources of the reviewee, but simply a comment on the paper. You will soon see what publishing a paper in a glamour journal means and you will not like it. Perhaps the worst thing about the process is the number or unnecessary experiments and their cost which do not advance the paper (on this see the almost classic : http://www.nature.com/news/2011/110427/full/472391a.html). A few comments and an editorial decision is what should happen. As we have seen this is what it used to be and maybe we should go back to go forwards. I wish the examples of EMBO J and eLife would be followed.

Then there is pre- and post- publication peer review. This is, like anything to do with this issue, a huge subject so I shall summarize. Many people advocate for postpublication peer review and to a large degree this goes on, in private, at lab meetings, tea rooms, discussions at meetings. But there is no will to do this openly. Most journals have now, routinely, places for comments which are not used. As we heard earlier: why are happy to write an impromptu review of a restaurant, a hotel or a book but we cannot do it with a piece of scientific work? What is wrong with bioscience? The only public comments that are allowed are positive. It seems to me that the notion and escalation of anonymous peer review has much to do with this situation. What we have is fear of backlash from criticism. The STAP case is a good, positive example of the cleansing power or open discussion of results. There is also a case for prepublication peer review but for these there are venues: preprint servers. As usual, for all the talking what happens is less than what one might expect. Preprint servers are not bursting at the seams. Lots of talk, but less action. The reason is because, for the most part, the scientists that make this tick are sensible and to prepare a manuscript takes time and care. The so far limited use of those servers, and the limited interest of bioscientists in them, should also be food for thought but, in any case I repeat my advice: use them!

Untitled.005-001And, of course, we need peer review. But we need to recover some sanity. We need responsible editors who do not fall prey to the endless sequence of reviews which cost money and careers, and we also need sensible reviewers who understand what reviewing a paper is and, especially, that it is not a way to block a piece of science seeing the light. We need to remember what a scientific article is and remember that it is the work that matters, and if you want to see more of the future let me tell you about another important development: San Francisco Declaration on Research Assessment (SFDORA or DORA for short).

In 2012, at the annual meeting of the American Society for Cell Biology, a group of publishers and funders signed a declaration, SF DORA, in which there is an explicit statement for “a pressing need to improve the ways in which the output of scientific research is evaluated by funding agencies, academic institutions, and other parties” (http://am.ascb.org/dora/). The main point that DORA wants to press home is that people should be judged by what they publish and not where they publish. To date the declaration has been signed by over 10,000 individuals and over 400 institutions. My advice is sign and, more importantly, enforce it. Make sure that those who have signed it, abide by it. What DORA says is obvious and it is surprising that it needs to be said.

And so to the future

The point of this lecture was to discuss publishing in the biosciences, why you might want to publish, what you would like to publish, how would you like to publish it and also where to publish. We have seen that answering these questions is more complicated than you think at first sight. There are two main reasons for this, the first one is that publishing today is not just a way to reveal and share our work but rather a complex action which will impinge on our future and job prospects, and one that is not straightforward. Together with this there is the fact that, in contrast with the science itself, the structure of scientific publishing has not changed much over the last hundred years and that therefore we are working with a system which is not only overloaded, in terms of supply and demand, but also, simply, not fit for purpose. As a consequence of this and, really, because of the impact where you publish has on your career prospects, there is a very open debate and scrutiny of the publications system and associated issues. There are many ideas around as to how to change it, and change is happening –slowly- but it is happening. So, where is all this going? To predict the future is always difficult but to close I would like to enumerate a number of elements of the tangle which need to be addressed for change to happen

1.The system of assessment of our work by the journals has to change. The way papers are reviewed by editors and reviewers and the roots of high rejection rates need to be reviewed. Some creativity and leadership is needed here and I would suggest that eLife and EMBO Press have made interesting steps in the right direction about this.

In this context if a reviewer wants to have an extended discussion with the author i.e exceed a certain length in the review, and suggest new experiments (which mean money), the identity should be revealed and the author of a manuscript should be able to have a proper discussion of what is being suggested to see what is reasonable. Like many I suspect that having to reveal the identity will change the tone and the content of the review.

2. Journals should implement seriously their policies of ‘conflict of interest’ and at this, they should make sure that their editorial boards do not have members that are also in multiple editorial boards of competing journals. This will ensure a commitment of the editorial board members to the particular journal and will, also, expand the group of people that make decisions about the content of those journals.

3. The journals have to adapt to the times. Supplementary Material was another added on to the operating system and as could have been predicted, it has got out of hand. Journals like Nature and Science now publish incomprehensible short papers where the actual science is in the supplementary. The reason why the text of many of these papers is gibberish is because it has been fragmented in the reviewing and publication process. Journals need to find new ways of conveying the science and a way to normalize the size and content of a paper i.e they need to adapt to the times.

4. Science is made by the scientists and it is for the scientists. There is a trend, promoted in particular by Cell Press, of dumbing down the science, of favouring impact and headline over content. Of favouring certain authors who frequent meetings and editors. Pieces of research become stories and journals rather than reporting advances, tell stories about genes and proteins and it is how you tell a story, rather than the content, that begins to matter. This could not happen in Physics but biology lends itself to this (and if you don’t believe it remember Rudyard Kipling’s ‘Just so stories’ some of which, with added materials and methods, could work well in Cell Press.

Journals need to take us seriously, we need to take the journals seriously.

5. If journals, particularly the generalists, want to keep their clout, they have to be more stringent on how they choose and train their editors. Teaching how to be an editor rather than learning it on the trot should be compulsory. In an increasingly professional world it is surprising that the main qualification to work on those journals (Nature, Science, Cell) is not to like, be bored with or have shown inability in the subject matter they are going to decide on. Imagine that the main reason to become a Chef is that you are bored with cooking or do not have a palate…… There should be a form of professional qualification for scientific editors e.g a masters on the subject (maybe there are). The consequences of the way editors are selected are clear for all to see. This can and should change.

But in the end, and for change to happen, WE have to make choices. At the moment we have chosen to emphasize form over content and science has become a routine mixture of salesmanship and one-upmanship, a power game where a few have an advantage. There are lots of meetings and lots of papers, but (with some exceptions) very little discussion and certainly open discussion. In public, all papers are great, all findings are exciting and there are lots of breakthroughs. In private, the picture is different. Part of the reason for this is that we have substituted questions and science for data presentation and therefore there is little conceptual to talk about. There is also the problem, allow me to emphasize, that the journals that drive the most visible biosciences are run by people that are inexperienced at both science and publishing. My advice is always, to avoid those journals. As long as we continue to search for their endorsement as a proxy for scientific quality, we shall be delaying change and we shall continue in a path towards forgetting the heart of the scientific quest.

The future belongs to you, so: make sure that you see it before it catches up with you. Nowadays the form of science is as important as its content and for this reason you should make sure that you shape it, that you don’t let the shaping to others. Open Access has become normal, let us make sure that other aspects that need change also become normal. Move away from glamour journals and towards journals that are led by scientists, use preprint servers, be open, careful and mindful when you review papers and grants (don’t do a review that you don’t want to see yourself), implement DORA. Let us make sure that science gets back to a normality adapted to the times.

PS: I was about to post the second part of the lecture when I heard the news of the suicide of Y. Sasai. This needed some pause and reflection. To many of us who worry about the current trends in the biosciences, the STAP affair has highlighted much of what is wrong about our enterprise and this is why I dedicated a part of the lecture to it and so did some of the other speakers. Whatever happened and whatever the reactions and possible consequences nobody would have thought of this end (so far) because a human life, and the blurring of a tremendous scientific reputation built over years of hard work, is not a prize to pay for the search of notoriety gone awry. Reflecting on this we should also remember that the chase of a publication in Nature, Science or Cell has many casualties we rarely hear about in the form of careers, enthusiasm, personal lives….while science was at the heart of the STAP affair, it was the search for the limelight that was its Achilles heel and, of course, Nature was only too happy to collaborate. Their job is to sell their product. It would be good if, as a community, we would think about how this came about and take corrective measures because otherwise our endeavour will lose its meaning, if it has not lost it already.

Additional miscellaneous reading

Kreiman, G. and Maunsell, JR.  Nine criteria for measuring scientific output. Front Comp Neurosci.5, 1-6.

Pulverer, B. (2010) Transparency showcases strength of peer review Nature 468, 29-31

Segalat, L., (2010) System crash EMBO Reports 11, 86-89.

van Dijk, Manor, O. and Carey, L. (2014) Publication metrics and success in the academic job.  Curr. Biol. 24, R516

Vale RD. Evaluating how we evaluate. Mol Biol Cell. 2012 Sep;23(17):3285-9.

Vosshall, L FASEB J. 2012 Sep;26(9):3589-93. The glacial pace of scientific publishing: why it hurts everyone and what we can do to fix it.

Williams, E., Carpentier, P. and Misteli, T. (2012) Minimizing the “Re” in Review.  J Cell Biology 197, 345-346.

Publish: What? Why? Where? How?

Untitled.001-001

These are notes for a lecture given by AMA in a workshop about Responsible Research held at LMU in Munich (Germany) on 24 July 2014 (www.responsibleresearch.graduatecenter.uni-muenchen.de/index.html). The lecture is broken into two parts, this one deals with biomedical publishing, its origins and current state. A second instalment on solutions will follow. Videos of both the lecture and the subsequent panel discussion are available at www.responsibleresearch.graduatecenter.uni-muenchen.de/presentations/videos/index.php 

The answers to the title of this talk should be obvious. You want to publish your work in the most appropriate journal/place so that people know what you have done, use it in their research and ponder the consequences. As we shall see, like much of the biomedical sciences (and it is this that I shall refer to when talking about publishing), the answers are less straightforward and you should think about every one of them. None of this was a consideration for F Miescher when he discovered nuclein (later known as DNA) and in 1869 wrote a paper which he submitted to the journal of his boss Hoppe Seyler, the Hoppe Seyler Zeitshrift fur Physiologische Chemie. Hoppe Seyler found the finding of P and N in an organic material so remarkable that he refused to publish it until he had observed this himself; now this is proper peer review. Two years later, satisfied with his own experiments, he published the paper –and one of his on the subject to support the observation. Much to ponder here –notice that he did not scoop his pupil- but I will leave you to think about it. The delay, the publication, the interactions with Hoppe Seyler did not have much of an impact on the career of Miescher.

How much things have changed! Today biomedical sciences publishing is, like many other aspects of the field itself, in turmoil; subject to debate not just in the scientific arena but also in magazines and papers. The Economist and the Wall Street Journal, not to mention the New York Times and The Guardian, periodically raise issues about scientific reports, in particular the biomedical sciences. The reasons for this media attention are complicated and you have heard about and discussed some of them earlier in the day but essentially boil down to a complicated tangle that has emerged between publications, jobs and money. Matters like peer review, the process whereby a scientific report is judged to be suitable for publication, have become under scrutiny and perhaps it is not surprising that last year one can find over 1500 and rising peer reviewed (notice the irony) publications on peer review in PubMed (where there were less than 500 ten years ago), with many thousands more in blogs and comments in journals. Why? The main reason is that, as we all know, a publication today is not so much about reporting progress on experiments and findings but about jobs, about grants, about careers, about upmanship. Publications have become, without us realizing it, the token whereby we are judged and ranked. There is a rather poisonous knot here that I shall try to untangle in the second part of the talk. First, let us get some perspective on peer review, the axis of modern science reporting.

It surprises me that we use papers like the famed Watson and Crick manuscript on the structure of DNA in Nature (by the way there were two other papers in that issue, one by a Rosalind Franklin) as a reference of something wonderful which, if possible, should be imitated. That paper would not have passed the editors desk nowadays and the famed sentence at the end: ‘it has not escaped our notice…..” would only have served as a ticket for the editorial rejection paraphrased as “it has not escaped our notice that while this is an interesting speculation, it would be important to get some experimental results to support it”. Sure, the topic was hot but, under today’s editors, the paper was a speculation on somebody else’s data and should be published, if at all, in the hypothesis section. Whereas in the 1950s science publishing was a small business catering for a small science community, today science is a very large enterprise and, I would say, publishing has not kept pace in the right manner. The fact is that today, the whole publishing business is a tangled web that results from growth without design. What do I mean by this? How did we get here?

Untitled 22.002-001There has always been some control over what people wanted to publish, and before the Renaissance, and also afterwards, the catholic church had that power. After all this is what Copernicus and, most famously, Galileo had to endure if their papers, books at that time, were not to the liking of the church. Copernicus was most careful but Galileo was obliged to recant his beliefs in public under the threat of torture; a rather stern form of rejection. Think about it, today your paper is not published, in those days if the reviewers did not like the paper you could lose your life. There is some progress!.

In more enlightened countries where the catholic church was not such an obstacle, Science (Natural Philosophy as it was called) was flourishing and some learned societies emerged to cater for this. Amidst these, the Royal Society of London. More of a gentleman’s club in the beginning than a society, it was a place in which people with a Science inclination got together to discuss what they were finding. People got into the habit of writing up reports and the Royal Society produced a repository for those reports: Philosophical Transactions of the Royal Society (1665) which is still being published today. Nothing new here, as at the time there were many different places where people could publish their observations and disquisitions e.g Acta eroditorum and Miscellanea curiosa. The Philosophical Transactions was another one but one which attracted the best in Europe. For example, it was here where Leeuwenhoek published his letters on what he saw down his lenses. The procedure was simple: you submitted a report, a scientist had a look at it and put it to print to be read by the people who were interested. It was here that, as the number of reports increased, the first hint of peer review appeared in the form of people, associated with the editor, who had a say on what had been submitted; basically making sure that it was not silly. But peer review in the sense of an external person to the journal checking the work was first used by the Medical Essays and Observations of the Royal Society of Edinburgh (1731). This kind of light touch review, mainly through the editor or someone very close to the editor of the journal, was adopted by the modern Science journals in the XIX century and this is the way in which Miescher and Mendel published their works. Another way to publish was books and this is, of course, how Darwin published his great work. No, his book was not peer reviewed though he did have what today we would call postpublication peer review. And a lot of it. Can you imagine what would have happened if Darwin would have had to subject himself to word limit, supplementary material and, above all, peer review?

Untitled 22.003-002And so, by the turn of the XX century the industry had not changed that much and the small enterprise that was science put out their findings in small journals, run by editors with an interest in science. Nature had been born in 1869 and the Elzevir family began publishing books in the XVI century becoming Elsevier (home to The Lancet and Cell) in 1880 and Science was founded in 1880. The bunching around the late XIX century is not a coincidence, it is a reflection of the rise of journalism and, within this, of the interest to get science to the public. The function of those journals was not to be the arbiters of a scientists career, as it has become today, but to get the scientific advances to the people. This is what hides behind that emptiest of lines in a rejection letter from Nature or Science: “your work is not of sufficient general interest….”. A vestige of a past in which, unlike now, such journals did sell to the people. In any case, in those days scientists had more specialized forums for discussions amidst themselves. It will not be a surprise to you that the mechanics of a scientific publication was different in those days.

Over the last few months, in the tangled discussions of Peer Review and as an act of rebellion, a famous incident involving Einstein is often quoted in the context of the negative effects of peer review (for a proper account of the event see Sean Carroll www.preposterousuniverse.com/blog/2005/09/16/einstein-vs-physical-review ). Einstein had submitted a paper to Physical Review on gravitational waves and the editor took the then unusual step, of asking for one referee report as he thought, rightly it would appear now, that there might be a problem with the work. When he sent the comments to Einstein for correction, Einsten’s reply was harsh:

“We (Mr. Rosen and I) had sent you our manuscript for publication and had not authorized you to show it to specialists before it is printed. I see no reason to address the ”in any case erroneous” comments of your anonymous expert. On the basis of this incident I prefer to publish the paper elsewhere”

Untitled.002-001And this he did. The point of the story is not the one people often quote it for. The point is that Einstein was right at being surprised to have the paper reviewed, because in those days, papers were not reviewed; certainly not in the manner that we do and understand today. Editors needed papers, often commissioned papers, and while they might make editorial comments, they certainly did not share the papers with anybody else. This type of review applied to the Watson and Crick paper and to the plethora of papers that form the basis of molecular and cell biology. However, as the number of scientists and papers increased and the material for publication began to accumulate, together with specialization, we start to see something more like the peer review process of today. Nature introduced a version of it in 1953 and implemented the seeds of what we have today in 1967. But The Lancet only introduced it in 1976! And with this small step, of a fair system to control the quality of what is published a complex machine is set in motion that today is a very complicated business, which can keep your paper going around in circles for up to two years in the high end of the market….the notion of high end of the market is, also a new development….basically, all has gone pear shaped. For a nice account of the life span of an average paper see S. Royle’s blog “some things last a long time” (http://quantixed.wordpress.com/2014/04/15/some-things-last-a-long-time/)

Untitled.003-001Many of us complain about the influence that editors have on the fate of the papers that we submit to them for publication. However, if you stop and think about the brief historical perspective I have given, you will appreciate that the relationship now is the same that it was at the end of the XIX century: editors decide what is being published. So, what is the difference? A number of things. The first one is that where the editor needed to find papers, nowadays they want to get rid of papers. The other one is that, in the journals that we could call ‘general interest’ where the editors were enlightened individuals with interest and knowledge, today we have basically a whole bunch of poorly trained scientists acting with a lot of power in their hands. The editor scientist has moved to more ‘specialists journals”. Today, more than ever, the generalist journals are not means to tell science to the people but represent a career asset, a ticket to a job and fame. But the other ingredient of the equation hat has changed is that where the editor (always in what I want to call the generalist genre) was an informed person making sure that the science got to the people, today is someone with the limitations derived from lack of experience and the size of the field, using more or less consciously a power they have. If you don’t believe me, read this post that will tell you how your science is not enough because it needs the editor to help you shape. This is certainly the view of Boyana Konforti (Cell Reports at the time of writing http://www.elsevier.com/connect/10-things-you-need-to-know-about-the-publishing-process) who states clearly that a paper is a collaboration between the scientist and the editor who, believe it or not, will help you tell and see a story. As she tells you: keep it simple! Sell a story! …….how low can we get? Are we writing for the editors? Is the scientific level of the editors what we should aspire to imitate? I guess what this is telling you is that if you want to publish your science, take it to ‘specialists journals’ run by scientists but if you want THE product that will give you a job, take it to them. This is where things begin to go pear shaped, where science departs from its original aim and where we have a disconnect between science and the journals. Particularly as I want to emphasize that those journals were not born to be the arbiters of science but to tell science to the people.

A recent case highlights everything that is wrong and dangerous about the situation and how the relationship between journals and scientists is sailing dangerously close to a storm.

STAP, a case in point (the perfect storm)

In January 2014 the journal Nature reported a remarkable finding. Somatic cells subject to a simple treatment (addition of lemon juice, as a friend of mine said), which involved stressing them in controlled conditions, could be reprogrammed to an embryonic state. This, the claim went, represented a huge step forward in the ability to produce embryonic stem cells as this would be natural and not involve the genetic manipulations associated with the Yamanaka cocktail. Furthermore, whereas the iPS cells are pluripotent, STAP (Stress Triggered Activation of Pluripotency) were totipotent, as they were able to give rise to extraembryonic tissues in addition to embryonic ones. This was a remarkable finding and because of this there was not only excitement but also suspicion. The simplicity of the experiment and the wide availability of cell lines with appropriate markers led to a widespread interest in doing the experiment –we did think of including it in our undergraduate project repertoire-. The papers were published by Nature and they had important and tested names most notably Y Sasai, H Niwa and T. Wakayama amidst the authors. So, what could go wrong? The first author Obokata became a celebrity and Y. Sasai, corresponding author in the main paper, was only too happy with the outcome. Maybe it was all too good to be true.

We live in the era of social media which has empowered people to speak. Paul Knoepfler, a stem cell biologist in California (USA) runs a blog on stem cells (http://www.ipscell.com/) and from the beginning expressed some scepticism on this finding. He set up a crowdsourced section in his blog where he proposed to report on attempts to reproduce STAP. At the same time he ran a periodic poll on whether people believed in the finding. In February, hope was high and the yeses outnumbered the noes. Slowly, the site was filled with failures to reproduce the finding. What is more, people in websites started to report issues of figure manipulation and text plagiarism which began to raise suspicions on the work and all of a sudden the limelight was on the first author. The web is full of what followed (see sources below) but by the end of May things were not looking good and by the beginning of July the papers were retracted because it became clear that the experiments were fraudulent. The big names put the blame on Obokata, who by now was under a huge amount of pressure (and has been ever since) and Nature claimed innocence. There was one most serious consequence of what happened here. The CDB, the host institution of the researchers, became under close scrutiny and in a surprising development, RIKEN the funding body, recommended its closure. The ball is still in the air but one hopes that the actions of individuals are not taken against an institution which plays an important role in modern developmental and stem cell biology.

The STAP case represents a collusion of interests, jobs, grants and limelight. The details and ramifications of this affair are too complex to dissect here, and I am sure that there will be books and analysis on the matter. Happy to answer questions at the end. There are nonetheless elements that are worth emphasizing. What could have happened here? I am not the only one in thinking that somebody, Obokata perhaps, did see something like STAP at some point. We all have seen black swans in the lab at some point; the problem is that they don’t breed, so we move on. In fact TH Morgan in his book on the Genetics of Drosophila has a section on ‘non heritable characters’ to quote an example. The magnitude of the possibility that harbours the finding and pressures from different sources that ensue then lead to the slippery slope. A group of people see glitter where there is dust and then you get the package: no questioning from above (if you understand Japanese you might be interested in this, and if not and you are interested, get someone to translate this for you: http://headlines.yahoo.co.jp/hl?a=20140416-00000024-wordleaf-sctch), the seal of approval of the big names, the seal of the big journal and, somewhere, the hope that somebody will see it again. I do not think that someone would expose themselves in the manner that Obokata did, unless there is some truth, and I suspect that she thought that somebody would see another black swan. How much Sasai, as corresponding author, knew is difficult to say but the fact remains that he signed as corresponding author. Much to ponder here on the structure and responsibilities in modern science. Ultimately the problem is that what was driving this affair was not science but the limelight. On the other hand, what brought this out was not just the scientists, it was the scientific community through the open discussion provided by social media, which has empowered people. And what responsibility with Nature? More than they are prepared to admit. They claim that the peer review process could not have picked up the problems (www.nature.com/news/stap-retracted-1.15488), but it was the science community which picked it up!. Furthermore, the manuscript had been rejected from Cell and Science. Furthermore, a quick standard run of the manuscript through image manipulation software run by EMBO J picked up problems almost instantly (http://onlinelibrary.wiley.com/doi/10.15252/embj.201489076/full). So, what one can conclude is that Nature’s peer review process, not THE peer review process, failed to detect the problems. As Nature refuses to provide details of the review process, we do not know what happened, but the refusal to be open (perhaps reasonable but not justifiable) does not help.

Now, this is not the first time that something like this happens in one of the main journals. Nature, Science and Cell have had their share of high profile retractions. In a remarkable one a few years ago, JH Schoen retracted 8 papers from Science and 7 from Nature (not to mention several from prestigious physics journals). This highlights the problem because as has been stated, the issue here is the scale which highlights the depth of the problem. How come that the journals do not take any impact? Have you heard of any editors resigning out of any of these affairs? Have you heard of the journals closing, receiving public scrutiny? Imagine that they were companies trading in the Stock Market. If something like STAP happens, and happens repeatedly, what happens to the shares? What happens to the company? And yet, in these journals nothing happens.

Where are we?

In the end, what we have is a situation in which these generalist journals have a different aim from their original one. Where they (though I should point out that Cell does not fit this mould) meant to be a vehicle to get science to the general public, they have become a, THE, measure of success. In fact, in China this is made clear in terms of outright payment proportional to where you publish (http://scholarlykitchen.sspnet.org/2011/04/07/paying-for-impact-does-the-chinese-model-make-sense/ ). But do not be surpised, as pointed out earlier, in Europe and the US we offer something much better: a pension!

We, a collective we, have used Nature, Science and Cell to create a rock star culture which has eroded into the base of what we do. The main reason for this, I believe, is the fact that the structure of the system we are using is, basically, the same as it was in the XIX century to which we have just added layers without restructuring it. An overloaded camel at the end of a long trip. This, together with a change of emphasis and aims, leads to  a machine that churns out papers with a lot of power in its hands and under the control of ill-prepared professionals which, basically, follow orders. NB I am not discussing here scientists led journals, some of which have a few of the same problems but which certainly do not have the ‘impact’ that lies at the heart of the malaise.

Fortunately we are waking up and solutions are on the way. In the final part of this discussion I want, briefly, to address some of them.

 

Additional Sources

Burnham, J. (1990) The evolution of editorial peer review. JAMA 263, 1323-1329.

Cyranoski, D.(2014) Cell induced stress Nature 511, 140143.

Kronick, DA (1990) Peer review in 18th century scientific journalism. JAMA 263, 1321-1322.

Nielsen, M. Three myths about scientific peer review (http://michaelnielsen.org/blog/three-myths-about-scientific-peer-review/)

Normile, D. and Vogel, G. (2014) STAP cells succumb to pressure Science 344, 1215-1216.

Spier, R. (2002) The history of peer review process Trends in Biotech.8, 357-358.

On the Schoen affair, take as a start: http://en.wikipedia.org/wiki/Sch%C3%B6n_scandal but there is much more on the web.

Very readable, interesting and informative history of Nature magazine: http://www.nature.com/nature/history/timeline_1860s.html

On Elsevier, with its long and distinguished history: http://www.elsevier.com/__data/assets/pdf_file/0014/102632/historyofelsevier.pdf

 

The unbearable lightness of being a developmental biologist at the start of XXI century

Let us play a game. Here you have three selections from the recent indexes of three famed journals publishing in the area of Developmental Biology. See if you guess which belongs to which (sure you can put the titles in PubMed and you will find them, but try to do it blindly):

Index 1

1. Large hypomethylated domains serve as strong repressive machinery for key developmental genes in vertebrates

2. Homeotic Function of Drosophila Bithorax-Complex miRNAs Mediates Fertility by Restricting Multiple Hox Genes and TALE Cofactors in the CNS

3. KFoA, a ß-catenin interacting protein linking canonical and non-canonical Wnt signalling during mouse gastrulation and tumorogenesis

4. Actin Cytoskeleton Reorganization by Syk Regulates Fcγ Receptor Responsiveness by Increasing Its Lateral Mobility and Clustering

5. Phosphorylation of CDK2 at threonine 160 regulates meiotic pachytene and diplotene progression in mice

Index 2

1. PIWI homologs mediate Histone H4 mRNA localization to planarian chromatoid bodies

2. Without children is required for Stat-mediated zfh1 transcription and for germline stem cell differentiation

3. Vegfd can compensate for loss of Vegfc in zebrafish facial lymphatic sprouting

4. Gene expression profiling identifies the zinc-finger protein Charlatan as a regulator of intestinal stem cells in Drosophila

5. The DEP domain-containing protein TOE-2 promotes apoptosis in the Q lineage of C. elegans through two distinct mechanisms

Index 3

1. Actin Cytoskeleton Reorganization by Syk Regulates Fcγ Receptor Responsiveness by Increasing Its Lateral Mobility and Clustering

2. RagA, but Not RagB, Is Essential for Embryonic Development and Adult Mice

3. Shh Signaling Protects Atoh1 from Degradation Mediated by the E3 Ubiquitin Ligase Huwe1 in Neural Precursors

4. D6 PROTEIN KINASE Activates Auxin Transport-Dependent Growth and PIN-FORMED Phosphorylation at the Plasma Membrane

5. Developmentally Regulated Elimination of Damaged Nuclei Involves a Chk2-Dependent Mechanism of mRNA Nuclear Retention

It is difficult. It is difficult even to guess which tier (of glamour) do each of them belong to. Rest assured that the abstracts would not help either; they all read the same and yet, when you reveal the brands attached to each of them, turns out that one of them will give more brownie points in job interviews than the other two; and one of them will not give you any points at all -answers later on-. But before getting to the point of this post, apologies to the authors of those papers (if any of them reads this post) for picking them; it is the result of random sampling. They are all good papers and any others would have served equally well. In fact, this is one of the points I want to make: it really doesn’t matter because the intrinsic value of a piece of research does not appear to matter these days.

The first point I want to make concerns the titles, the topics, what is happening to developmental biology. The titles are variations on the theme “gene X/motifM in protein B is required in cell type Y for this/that/ or the other”. Ever since mutant screens took hold of the field, the aim is either to identify new genes and link them to known functions or processes, or to find new functions for known genes (signalling pathways get a prize here). The emerging alternative is those high throughput maps that reflect the toilings of a lot of people, which we are supposed to mine. There is little doubt that this is useful but, is it interesting? Sure, we need to do an inventory of the genes, their products and their modifications and link them to phenotypes but, is there a challenge here? Are there not interesting questions left to answer? I agree that there are technical challenges but, for the most part, these can be dealt with and a product will emerge, a formulaic one. Most papers look like each other, though in the discussion sections there is a bit more latitude in how the results are framed but, for the most part, they are all the same; another piece of a large puzzle, a puzzle whose template we have lost a long time ago. There are problems out there, there are large questions but nobody pushes us to think about them. I have discussed some of these issues before (http://amapress.gen.cam.ac.uk/?p=1094); all I will add here is that slowly, our enquiry is becoming light, unbearably light for those who want to know about and address important issues, or who want to hear those issues. The real questions, that exist, are being diluted by facts.

Thirty years ago we wondered what was the nature of the genes that mediated developmental processes. Many people tackled this question from different perspectives. Some never went anywhere, some did. C elegans and Drosophila brought genes to where chickens and frogs had laid questions and this provided answers to problems. It was (still is, as far as I am concerned) amazing the way it turned out: that the genes we identified in worms and flies had a bearing on vertebrates. But this was, with perspective, satisfying because it meant that there are rules, principles and today, though the indexes of the journals might betray them, we thrive on those principles. With the passing of time, the questions and the answers have become light. Driven by referees, editors, increasing meetings of hype and a general confusion of science with craftsmanship and technology, the lightness of the Science becomes unbearable. An apocryphal comment says that Science might end with us learning more and more about less and less and I am afraid that this is happening in Developmental Biology. If we are not careful, we might end up in the logical conclusion of that path: we shall know all about nothing. What are questions of interest? It will be good to identify them but two of my favourite ones lie in the emerging observation that cells churn out numbers and we do need to understand what those numbers are and where they come from. We need to know how the stochastic molecular world is averaged to the determinism of development and also what is the structure (not the hairballs that people call networks) of the machinery, the molecular devices that mediate the averaging. More on this in the future but here be dragons and perhaps this is why it is easier (but not technically) to carry on with the catalogues.

The reason for all this is that, for the most part the biomedical sciences have become a job which spins out other jobs, particularly in the journal business. I would claim that more than 50% of the publications in the areas of molecular, cell and developmental biology have as their primary aim to serve as career token. Some of them provide information but most of them are just registers of a job done. And here lies the reason why biomedical sciences is becoming unbearably light, because there is less and less hard science in much of what is being produced (read the indexes above). The ‘careerism’ and overcrowding of biomedical sciences is being discussed in several forums. Like many, I hope that we can find ways towards a solution that will restore ‘scientific enquiry’ to the heart of biomedical sciences (at some point I promise to discuss the relationship between the physical and the biomedical sciences which has some interesting lessons for us, biologists). And in this low grade industrial game we are playing, the most important things seems to be not the scientific value of the work but the ranking of the place where the work is published. Yes, I know, this sounds familiar. Time to get to the second point and disclose the journal to which the indexes above belong:

Index number 2 is taken from Development, index number 3 from Developmental Cell and number 1 is a concoction from three journals: Development (title 1), Dev Cell (titles 3, 4) and Developmental Biology (title 5) with a made up paper, did you guess it?, number 2. The point is indeed that they are all the same and that it really doesn’t matter how we distribute them. The titles I like are because they highlight what this journal game is about:

“Vegfd can compensate for loss of Vegfc in zebrafish facial lymphatic sprouting” and “RagA, but Not RagB, Is Essential for Embryonic Development and Adult Mice”,

essentially the same issue at stake. Different genes, different organisms, but the same. Almost mirror images of each other and yet, the paper in Dev Cell will give more kudos to the authors. Why? If there was ever a case for SFDORA I think this makes it clearly. It is the same product branded differently but a paper in DevCell will be looked upon as higher quality than on in Development or Dev. Biol. A recent observation in Google Scholar makes the similarity of the two journals more blatant: Dev Cell has an impact factor of 12 (not that great for all their bravado), Development 6.9 and Developmental Biology 4. However, if we looked at the h5-index we get an interesting perspective: Dev Cell’s is 89, Development’s 80 and Dev Biol’s 58. Difference vaporize, particularly between Dev Cell and Development.

googlecholar

One hopes that this will be noted. Not the lack of difference but the inflated nature of some perceptions. In the meantime, a “collective we” still fall for the gimmick of Cell Press (or Nature or Science). Their editors (and publishers), who engineer the game, will tell you that they have the highest standards, particularly in the context here those of Dev Cell. I remember talking to one of the big editors of Cell many years ago, suggesting that I did not like the way they were twisting molecular and developmental biology. This person said to me: ‘we don’t back any horses’. To which I replied that they did not need to, because they bred their own. They have now such a stable that they can organize their own races/conferences around it. It will be claimed that the papers in Dev Cell will have had a more tortuous reviewing process than the ones in Development, which makes them of higher standard, and that some of those in Development or Dev Biol might have been rejected previously from Dev Cell. Some of this is probably true (the rejections, the lengthy pointless review process) but do not be fooled, read the titles, the papers. The quality is the same and the advance that they convey –their scientific content- will also be the same. The difference is the marketing of the product and Cell Press is very good at selling their own. The kudos of a paper in Dev Cell is not based on the rigour, the novelty, the interest or the impact of the paper –as shown above- but by the marketing of the product. And, do not forget that indeed, it is harder to publish there, that the papers in Dev Cell will have more of a spin, that they will have costed more money (in revisions); but nothing else. It is a bubble (remember the tulips in Holland in the XVII century: http://en.wikipedia.org/wiki/Tulip_mania) and we should burst it. Cell Press is general is mostly tulips.

In the end, coming back to the science, none of the journals discussed here address or deal with real problems, with serious questions. This is not for lack of these, it is that the real issues don’t sell (apparently this is what these journals want to do) because they might not have an easy answer, because they cannot solve the problem in a marketable way. What does a journal rather publish: “gene Z controls DNA repair and HXYAc in development and cancer” or “the process of time averaging of gene expression cannot be explained by epigenetics”? The good news is that we see less and less screens at the forefront of the journals, the bad news is that this is being substituted by an ever increasing catalogue of more or less interesting but certainly unbearably light assessments of the functions of genes. A lot of work but, for the most part, facts in search of a reason. And most of it driven by journals, with their impact factors relish. Techniques should answer questions not hope for questions.

Solutions? The key lies in the attitude of the current generation of postdocs and graduate students since the future belongs to them. Some things are not going to change but there is something that needs changing: we need to recover the control over what we do, we need to get rid of the tyranny of the journals and the editors. An involuntary collusion of funding bodies and journals has created a very complex atmosphere in the biomedical sciences which has trivialized the science. We need to prise back from them what is ours. SFDORA is one step in that direction and I am constantly surprised how little known it is within the postdoc community. SFDORA is, at the moment the only forum which we can fuel to begin to solve the problem. The other is, of course, a bit more difficult as it relies on thinking what are the real issues in modern developmental biology. But perhaps what I sense as an unbearable lightness in the field is because there is nothing else of interest to be found out…….I don’t think so.

 

New Paper

 

paper_abstract

Our manuscript “An interplay between extracellular signalling and the dynamics of the exit from pluripotency drives cell fate decisions in mouse ES cells” in out in Biology Open (http://bio.biologists.org/content/early/2014/06/13/bio.20148409.full). We tried a more ‘conventional’ journal but we were told, basically, that there were no new genes. As the editors of this august journal were correct, we opted for actually publishing our findings and submitted to Biology Open where we got an effective, fair and constructive review process.

The manuscript has much that is new and of interest as we use an integrated approach with different experiments to understand how Embryonic Stem cells begin to make decisions as they exit pluripotency. There is much that is new and, perhaps of interest, here and we suggest that if you are interested in cell fate decisions and the way signals steer cells into particular fates, have look at it.

An interesting (we think) notion is that of a molecular race in fate decisions.. We believe that this might be of wider applications than just at the exit of pluripotency. There is also a novel view of the role of Wnt at this juncture.

For Website Biology Open.001-001For Website Biology Open.003-001For Website Biology Open.002-001

 

Modern Biology and its tower of Babble

 

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Reading the index of some glamour journals made me think about the Tower of Babel. The famous story starts when life on earth had got under way after The Flood and the surviving human beings decide to build a very large tower that reached into Heaven to challenge God. There is a lot of Biology in the Bible and it is stated that, at this time, all human beings –being derived from a founder effect due to the ‘Noah population bottleneck’- were similar, spoke the same language and shared purpose. Not to digress, the work goes well, helped by the common language. One day God has a close look at what is happening: the project is going swell and there might have been other projects on the go in the same direction. God senses danger (some call it pride) and reckons that the reason for the progress lies in the homogeneity of action through a common language. Worrying that humans might get too big for their boots decides to do something about it -remember that the God of those times is not that kind- .

“If as one people speaking the same language they have begun to do this, then nothing they plan to do will be impossible for them. Come, let us go down and confuse their language so they will not understand each other” (Genesis 11:6, 7)

As a consequence of this action, people start not understanding each other and progressively break up into groups. As the common purpose and the ability to communicate disappear, the work ceases, the tower is abandoned and humans disperse across the face of the earth. Other projects will appear in due time, but less ambitious, more pedestrian.

One sees elements of what is happening nowadays in Biology, with some consequences. Where a while ago we had a common language manifest in a set of focused significant questions which we could all understand and address together (what was the basis of inheritance, what is the material basis of evolution, what is mechanism whereby a gene effects a structure, or the genetic basis of developmental processes), today we have a collection of fields, each with its own language and aims. Chip-on-Chip, Chip-Seq,  TALEN, CRISPRs, CRISPR-Cas, SPIM, STED, FCS, FACS, MS, LC-MS, SPS-MS, iPS, H3K27m, HDACs……. (see how many you recognize) …….  We seem to have been cursed in the way it happened in Babel but with the difference that we still have not realized what is happening (maybe it also took time in Babel for the realization). In fact we seem to be proud of this babble and, to a large degree, thrive on it. These acronyms have created fields like epigenetics, proteomics, stem cells, recombineering, etc which are like organisms that need feeding and the food is papers with data disguised as science but whose only goal is to fatten the journals and provide a sense of satisfaction to the authors (ah yes, and a salary to the editors). I am not saying that there is no good science around but I am saying that one has to dig deep to find it. And some researchers have become very good at selling what they do, which means that the disguise can be very very good. Journals give Babble a seal of Science.

Recently a colleague was going to have a journal Club on a paper in a hugely glamorous journal by one of those authors who can publish there (don’t forget that ‘all authors are equal in the eyes of the editors but some authors are more equal than others”). The title looked appealing and the abstract involved the now usual cocktail of words that such journals like of high throughput chromatin modification, names of usual genes in the said journal, the obligatory inflationary reference on Twitter to the work……… The day before the Journal Club, it was cancelled: everybody agreed that there was nothing to discuss. The manuscript was a list of genes, some loose/forced correlations with function and a failed attempt to make sense of some of the genes in the pool. This is not unsual. The more glamorous the journal, the more likely it is for you to find this kind of manuscript: lots of data whose quality one has to take for granted, no real question, an attempt to find some correlations between the variables scattered through the paper and very little else. Just have a look at the indexes: Gene X is involved in the differentiation of cell type Y, ZZZ confers polarity to the developing RRR, a new VV-modification in the genome/protein/DNA of YYY and so on…..cataloguing at a level of high resolution.

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As in Babel, having lost a common language, the emerging pidgins lead us to forget the possibility of doing something important, of tackling real problems. Instead we fall into cataloguing the connections of the brain, the genes of 10,000 humans, the genes involved with Cancer…these are useful projects that get the limelight, capture the imagination of the politicians and the funding. Enquiry of the form that led us to find out about the action potential, the nature of the gene or the chemical basis of metabolism is not deemed fundable and as a consequence, training in the art of scientific enquiry falls by the side. I am not saying that what is favoured today is not right or good, on the contrary: it has its place. What I would like to say is that we should get some perspective and do things right. That in addition we should find a niche for what some of us will defend is real science that will make the enterprise much more meaningful. Some funders will say that this is what they do in some schemes but what they do is to fund more of the same. 

Sometimes I like to think about the Manhattan project as an example of how, when there is a common purpose and one can create a common language, interesting things happen. Most people know the Manhattan project as what delivered the first atomic bomb. And this is correct. What most people don’t know is the scientific and technical challenge that this posed and how on the way to create that most terrifying of weapons, a great deal of science and engineering was spawned out. Under the pressure of delivering a common goal, many existing problems were solved and others were created. Physics, engineering and maths benefitted to the point that as Oppenheimer said “physicists have known sin, not because they built the bomb but because they had fun building it”. The reason why they had fun is because they had common challenges to solve and they worked together towards them. Theoretical physicists worked alongside engineers to answer questions which sometimes would have a practical end but sometimes they would not. I know no current biological project that can mimic the Manhattan project because many of the ones that are around are just large scale data collecting exercises. There are some places with the potential to do something useful but the culture of superficial data gathering is too prevalent.

And so it comes to pass that Biology today is in the early stages of a fragmentation in which language plays an important role. It is the tower of Babel in the early stages of its disaggregation or perhaps, as a friend suggested the other day, God felt that we were getting close to his trail again and did a second Babel in the form of the jargon and babble that we suffer today. 

People work their niches according to narrow views that emerge through a feedback of journals-funding bodies-lobbies which, slowly will lead to new rounds of fragmentation. What determines a field is the technique, the language. Data and the way it is presented, is part of this language problem. Language has become the means to success in that if, within a field, you can string in a successful manner a number of words with some large amount of data, you will be successful. There is a catch though. It would be foolish not to recognize that, since Linneaus and Darwin, Biology does require a lot of data gathering and that often, it is not clear what data is needed for a particular question. So, to gather data is important but it is important to do it well, and to have a purpose. More importantly, we need to distinguish data gathering from science, and I am not sure that we are doing this at the moment. In a not too distant future the winners will be those who can mine the available data but only those who can see the questions, only those who remember the original language that was spoken in Babel and who have a memory of what was the point of the tower; only those will succeed (in the real sense of the word).