In this episode of Expert Insights for the Research Training Community, Dr. Alejandro Sánchez Alvarado, director of the Stowers Institute for Medical Research, discusses how to move into uncharted territory in research and study nontraditional research organisms.
The original recording of this episode took place as a webinar on May 5, 2020, with NIGMS host and director Dr. Jon Lorsch. A Q&A session with webinar attendees followed Dr. Alvarado’s talk.
Recorded on May 5, 2020
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Announcer:
Welcome to Expert Insights for the Research Training Community—A podcast from the National Institute of General Medical Sciences. Adapted from our webinar series, this is where the biomedical research community can connect with fellow scientists to gain valuable insights.
Dr. Jon Lorsch:
Hi everybody, this is Jon Lorsch, director of NIGMS, and I’m really happy to welcome you to the second of our virtual online webinars for the NIGMS and other training community. This is something that we decided to do since so many people are trying to work from home and to learn from home. We thought it would be a good idea to put together some seminars in different areas of interest to the community, we hope, and to try to engage people.
So, let me introduce today’s speaker and question answerer. It’s Alejandro Sanchez Alvarado, very well known to many. Alejandro is the scientific director of the Stowers Institute for Medical Research in Kansas City. He is also an investigator of the Howard Hughes Medical Institute.
He was born in Venezuela. If you want to learn a little more about his past, I would encourage you to go look at the regeneration issue of the Pathways magazine that NIGMS puts out in partnership with Scholastic, and you can find that at www.scholastic.com/pathways. That has a very nice little section on the back of the magazine about Alejandro and you can see a picture of him as a boy holding a very, very large anaconda, which I think is probably dead, but we’ll ask Alejandro afterwards, around his neck. And you can learn more about Alejandro and his career there, as well. It is designed for middle- and high-school students, but I think students of all ages should enjoy it.
Alejandro, after leaving Venezuela, came to Vanderbilt University, where he got his BS in molecular biology and chemistry. He then attended University of Cincinnati College of Medicine for his PhD in pharmacology and cell biophysics. Once he got his PhD, he went on to postdoctoral studies at the Carnegie Institution in Baltimore. And from there, he actually got an independent position at the Carnegie in embryology to run his own research group, which is where he started working on this really seminal work he’s done, this pioneering work, studying planaria and regeneration in planaria. I’m sure he’ll have something to tell us about how he started that work and why today.
He has been a pioneer and a promoter, a very strong promoter, of the use of non-traditional research organisms and the study of interesting and new organisms, at least new to science, in order to uncover unexplored and great discoveries in biology. He’ll certainly talk about this, that’s the point of this presentation, in this Q&A session. But if you want to learn even more about that, I encourage you to go to his TED talk, which is really fantastic. He talks about all the reasons that all of you should be looking at unusual organisms and thinking about unusual organisms in your research.
So I’ll just end the introduction with a quote from the Pathways magazine. It said, “Just what keeps Dr. Sanchez Alvarado so captivated: His answer is poetic. ‘I have a fascination for these very small and unheralded things. I’m certain they contain a large number of secrets waiting to be uncovered.'” So, Alejandro, thanks so much for joining us and I’ll turn it over to you.
Dr. Alejandro Sanchez Alvarado:
Thank you very much, Jon. I mean this is a great opportunity and a great event for me in this time where biology is actually dictating most of our cultural activities in the form of a little cycle of molecules that we’re now referring to as SARS-CoV-2. It’s great to also have the opportunity to chat with many of you out there who are, like me, very interested in biology and wondering, you know, what we have in the world around us that should be of really important interest to us, to all of us.
When Jon emailed me to ask me to participate in this, you know, he asked me to start with a few remarks of why I think that we are not really but scratching the surface of biology with our current activities and I thought this would be a really good opportunity.
And I’m going to just use a short period of time to give you the rationale for why I think that there’s a great deal of biology to be discovered. That if you’re a student, if you’re a trainee, that there’s a wealth of knowledge that needs to be mapped, that has yet to be discovered, and that there are a number of sociological constructs that in some ways are preventing us from pursuing those opportunities. And so, I’m hoping that during the question-and-answer period, we’ll be able to address some of this.
But let me just put things in perspective, just to give you a sense. You know, the brunt of everything that we have learned to love and appreciate in modern biomedical research, particularly in the life sciences of the past 30 years or so, has actually risen from the study of a handful of organisms, organisms that I always like to say they were not selected because they occupy the particularly interesting position in the evolution of multicellularity, for example, they were selected for practical and pragmatical reasons. Primarily, do they manifest a particular attribute that we can take advantage of in order to investigate a particular biological question?
This is really the beginning of experimental biology. You find an organism. That organism is suitable to address the questions that you have and you end up bringing it to the lab, growing it and then, you know, dissecting it, and extracting as much information from it.
And this particular practice of science became super, super prominent in the 20th century, to the point where it culminated by the selection of a handful of animals that are now, you know, the brunt of the species that populate pretty much almost every modern biomedical and life sciences research laboratory, not just in the U.S., but across the world.
These organisms are very familiar to you. Many of you may be working with them. These are animals like mice; fish; C. elegans, which is a recent newcomer; Drosophila; yeast; bacteria; and a handful others, like chicks and a few others, right?
And so, there’s a reason why these animals have been so successful. It’s because they were accessible to experimentation, you could generate a large number of progeny to be able to do genetics or you could generate large amounts of biomolecules to be able to study their functions and the like, and that became sort of like the trend.
It all started, I would say, with Morgan selecting Drosophila at the beginning of the 20th century. Then, that was followed by the utilization of guinea pigs and other small rodents, once genetics was really instrumental to really access the mysteries of biology. People began to look for vertebrates that would be amenable to genetics, so mice were a good animal because of the large number of progeny they produced, their relative small size, that they could be kept in the lab. And so, you know, it went for like, you know, guinea pigs, rabbits, rats, and, ultimately, you know, mice, right?
And so that’s what you begin to see. There are other organisms that, even though we may not have had genetics for most of the 20th century, were nonetheless instrumental in allowing us to understand developmental processes, like Xenopus, for example, another really workhorse of developmental biology because they produce lots of embryos, lots of eggs, and you can do a lot of biochemistry and molecular biology with this abundant material.
Now, this was a given, right, this was a given that if you invest and select a number of animals that appear on the surface to be very diverse and different from each other, that that should be enough for the sampling representation to encompass most of what you really need to understand in the biological world in order to be able to extract things like first principles, you know, understanding of how molecules talk to each other, how these molecules and molecular agents come together to provide behavior to the cellular agents that are actually going to execute functions and how the cellular agents come together to give rise to tissues, organs, individuals, etc.
But here’s the problem: The problem is that these organisms turned out not to be very different from each other. As the 20th century progressed and our understanding of evolutionary relationships between animals got better, and genomes began to be sequenced and their composition compared to each other, turned out that many of these organisms that were supposed to be very dissimilar from each other were actually very closely related to each other.
Examples are Drosophila and C. elegans, which as different as they look from each other, they end up being grouped in the same clade as Ecdysozoa. They were related to each other, cousins of each other. So, that essentially brought almost all of the animals that we work in the lab could fit into essentially one or two clades, a couple of species.
All of the vertebrates and our invertebrate relatives through Drosophila and C. elegans being part of the Ecdysozoa. That’s essentially, maybe, three phyla, three to four phyla, that we’re looking at, out of the 30 and growing number of phyla of animals out there. So, it is an under-representation of the immense biological diversity that remains to be understood.
It is hard for me as an individual to imagine that everything we need to know in biology is going to be represented by this handful of essentially randomly selected organisms from the wealth of life that exists in the planet. And so, the attraction for us in the 21st century is that the tortilla kind of flipped. It used to be that we really, really needed a lot of material, that we needed to domesticate animals in order to be able to dissect it molecularly, but as this is going on in the background, technology is also changing.
And technology has gone from being, like, this humongous, you know, infrastructure where you would need a whole building built just to have some electron microscope, for example, to a process of miniaturization and a need for even smaller and smaller amounts of material to do the research. But it all of the sudden has opened an unprecedented opportunity in the history of the life sciences, which is that many species out there that were either too remote or too few or very difficult to access are now accessible to a degree of interrogation that is completely unprecedented.
We now need micrograms of material, nanoliters of material, microliters of material, to be able to sequence genomes, define a single-cell expression profiles, define also the transcriptomes of entire, if not populations, individual organisms. And this is truly, truly unprecedented and it will allow, I think, for, in this century, an opportunity to not bring nature and domesticating into our labs in the hopes that we’re going to be able to understand the natural world, but do the opposite, which is to actually bring the lab into nature and understand how that life actually lives.
It’s not uncommon, if you ask many of our colleagues, to tell you about the natural history of the organism that they work with, and they might not know much about them. If I ask my colleagues working on zebrafish, “Have you ever been to the Himalayas and look at where the zebrafish animal you live with, that you work with, where does it live, how does it live, what kinds of behaviors does it display?”
Very few will be able to tell you, “Yes, I am familiar with the natural history.” C. elegans is the same way, Drosophila is the same way, even yeast the same way. It’s not really something that has been embedded in our approach to doing science to understand the natural history of these organisms. We just look at them as tools, as vessels that serve to, you know, dissect molecular and cellular processes. But I think the time has come now to understand how those vessels were built and those vessels were built in nature.
And in nature is where evolution chiseled, you know, the actual extent of species that we see today. And how does an individual species evolve in relation with the rest of the species that surround them is something that we really don’t understand.
So I think that there is a significant amount, you know, of material out there that we don’t understand. And I’d like to make the following analogy, which is that, you know, to work with the organisms that we have domesticated and we are using in our laboratories today and have been the workhorses of our understanding of developmental biology and cell biology, biology in general, I mean that’s like mapping already discovered continents.
But I’m actually convinced that there is a large number of continents out there to be discovered and I think that particular aspect of science, particularly in the life sciences, is something that has not received as equivalent amounts of attention as these other systems that have been developed.
So we have an opportunity now where technology and our availability to access these very small numbers of material to really push forward and push open, wide open, you know, what is it that we really don’t know about biological processes.
It’s remarkable, I mean, there’s so many things we don’t know in biology. We don’t even know what is possible and we’re always surprised when some new species comes out that does something really extraordinary and it violates the rules of the so-called first principles we have developed in order to understand, you know, how the biological world unfolds.
But the ignorance that we have in general about the natural environment that is actually chiseling and folding and refolding all of these molecules to give rise to all these different functions and all of these different activities and that still remains fairly mysterious, in my opinion.
And so, here’s my impetus, and my challenge to you, is that, you know, if you have a biological question in mind and you don’t think that there is a system already available that allows you to address that question, my guess is that there’s an animal out there, or a plant out there, or a fungi, or a bacteria out there that would actually serve as a vessel to try to address this particular question that may not be saliently and exaggeratedly manifested in the systems that are available today.
And I’m going to stop here and I will now leave the floor open for any questions that you may have.
Thanks, Alejandro, that was really I think inspiring and as they said in the magazine, kind of poetic, actually, and I hope the message resonates with people listening.
Alejandro, maybe you could start by telling us a little bit about, you know, you made this big jump, you know, kind of after your postdoc where you jumped into this, you know, essentially new and largely unexplored organism, at least at the molecular and cellular level, the planaria. What made you decide to do that and what was it easy or was it hard?
Yeah, so I got into planarians through a very circuitous route, very, very circuitous route. I discovered some point in my PhD, mouse embryonic stem cells, which at the time were being used as essentially a tool to do homologous recombination, introduce a mutation into the mammalian genome, and then see what would happen.
And my job at the time for my PhD was to try to target one of the cardiac myosin heavy chains, alpha beta. And so I was doing these transformations into these ES cells. I was making the little colonies and hoping that we could transplant those modified cells into a mouse embryo and then, hopefully, get a phenotype.
Now, being a graduate student that we all seem to be at some point in our lives, you know, I had some of these ES cells growing in a petri dish, and I sort of forgot about them and I left, right? And so I came back and I opened the incubator and in that petri dish, some of these ES cells had began to differentiate and they have come together to form these embryoid bodies and many of them were beating.
So, they gave rise to these beating embryoid bodies. I was completely fascinated by this, that a completely undifferentiated cell would actually be able to give rise to some semblance of form and structure. I think if we had called embryoid bodies “organoids” back then, I think we would have been very famous right now, but that’s not what we were thinking.
We were thinking, like wow, this is really astonishing. So, this genomic aqua plasticity that these cells were displaying, it really caught my eye. I mean, I wouldn’t call it “genomic plasticity” back then, but I mean I thought I was, this potency really caught my eye.
And so as I began to read about it, I began to think that maybe one thing I want to understand is how cells determine what they’re going to become. And one of these problems that became really apparent to me that wasn’t answered at the time was a problem of regeneration, where you have an already differentiated structure that you’re now going to amputate and you’re going to ask from those pre-existing differential structures to build something new, something that in principle had happened much earlier in embryogenesis.
So I like the notion of having this regeneration as a heterotopic and heterochronic double experiment. You’re asking an adult tissue to do embryonic processes and not just any embryonic processes, very specific embryonic processes to restore a missing structure and they have that structure, you know, functionally integrate into the preexisting structure. It really went to the root of like, you know, what’s an individual, what is old, what is young? I mean, how do you combine those things together?
Looking further and further into this, I realized at the time that there were no really good systems that would be amenable to type of molecular biology and genetics that would allow for a dissection of regeneration. And after a process of elimination, Jon, I literally, I still have the table.
I had a bipartite Tree of Life–this is before there were three branches–just two branches. And I went phyla by phyla looking for examples of animals that could regenerate. And everybody had told me that regeneration was an epiphenomenon, that it only occurred in a handful of organisms, it was a waste of time to study because if you study embryology you’ll understand regeneration, right?
And to my surprise, I mean, almost every phyla that I had literature for had examples of some sort of regeneration. And I became smitten with planarians. This was in Woods Hole I found a book written by T.H. Morgan called “Regeneration,” and the first chapter was on planarians and that’s when I discovered that Morgan himself had actually worked on planarians.
Up to that point, I thought he just worked on Drosophila. That’s what he’s famous for, Drosophila but he said biographers at the time had completely ignored all of his training before the Drosophila time. And Morgan was pretty much a zoologist and a botanist. I mean, the guy was a scientific polyglot in the biological sciences.
At the end of his existence, he had worked and published in at least 30 or 31 different species for both kingdoms, all right, so to give you the sense of the kind of training that biologists back then had. But that’s how it happened. You know, I came through it through a very circuitous way, and then I realized that, you know, planarians had not really been studied as heavily as other systems that I was familiar with the distylium or like fungi, like yeast, and the like and I wondered, you know, why not planarians and that started the whole thing, just looking into the system and so.
Was it hard to get this funded? You had this totally new idea.
Yeah, I mean, so here’s where I think that, now that I am on the senior-investigator side. I think what made a huge difference for me was not so much to get the funding, but to be able to have senior members of my community to see the importance of allowing individuals to pursue their own ideas. This is fundamental because when I first looked for postdoctoral positions and I was suggesting that I was going to work on regeneration, none of the labs that I was asking to work with were working themselves on regeneration.
Not to say that, you know, we as senior scientists really have to develop and protect ecosystems where young people can come and try their hands at new ideas, right, and so that was my first experience. I mean I thought that was normal. I thought that what people wanted you to do was to come to the lab and do your best possible science, right?
In retrospect, I realized that, you know, that I got fortunate enough to be able to identify such an ecosystem in the laboratory of Don Brown at the Carnegie Institution, where he essentially just gave me, you know, an open field. You know “Okay, that’s what you want to work on. I like your idea. Start working on it and then, by the way, just try to get a postdoctoral fellowship.”
So I did and I got an NIGMS, before it was called a Ruth Kirschstein award. I got one of those and that was what began to fund my research, not on planarians, but it was on a frog. Now think about how crazy this is. That’s why I think we need to protect these spaces.
Don Brown is known for developing Xenopus laevis as a research organism to investigate a large number of processes in biology from metamorphoses, to gene expression, gene regulation, and the like. Now think of this, a young guy with no track record, other than he just got his PhD, comes in and says, “Hey, Don, I want to work on regeneration. Oh, and by the way, I don’t want to work on Xenopus, I want to work on this frog that was recently published in ‘Developmental Biology’ by Malcolm Maden. It’s a European frog called Rana temporaria that regenerates its tail but when you cut the tails of the tadpole and you put them in a vat with, like, retinyl palmitate, instead of regenerating a tail, they regenerate hind limbs. That’s what I want to work on.”
And Don says, “Well, if you can get the frogs, why not?” And so that was my homework. “Find a way to get the tadpoles into the country because they’re endemic to Europe and do the work.” And that’s what I did. That’s what I did for about a year, six months to a year, in Don’s lab.
It never resulted in a publication, I never published this work, but it opened the door for me to think about, “If there is no system to study regeneration at the molecular level, we should develop one,” and that’s what led me to the position of eventually going to planarians.
And here’s the other thing, so once I had enough preliminary evidence that this might actually have legs, then I began to write grants. And I have to tell you, you know, I have a long list of grants that were declined, but I have a list of grants that were funded, and those are the grants that allow you to move forward. So, yes, it wasn’t, you know, impossible if the councils were slightly different, the pay lines were a little bit higher, but, nonetheless, you know, I have been able to, consistently been able to identify sources of funding to do my research.
You just have to get used to a lot of no’s and you have to, you know, try to shoot for those granting opportunities that you think will give you the best chance to propel your research forward. But it requires a great deal of persistence and a lot of colleagues, you know, that will help you read the grants, will, you know, give you encouragement when, you know, when your grant is triaged, is not even discussed. I mean, this happens to everybody, and I think one of the mistakes that my generation and past generations have done is that we have not shared with everybody our failures as much as we have shared our successes.
So it looks like we’re very, very successful, but that success is supported by a large number of failures. It’s just that, you know, for whatever reason people just love to hear success stories, but I think for our trainees, it’s important to understand that, you know, your best idea may not have necessarily, was not necessarily funded from the first start. And so there’s plenty of stories out there of people who try for years to get funding and they don’t, and turns out their ideas were terrific and eventually things work out. But it’s not a given that successful people had no failures or have a paucity of failures on their record.
So a number of questioners are asking, you know, along that same line, if they’re excited to go and study something completely novel, you know, a new organism like you described, but they hear a lot that, you know, you should do something safe.
“If you want to get funded, you got to do something closer to the pack.” Do you think it’s possible, and how would you approach, you know, moving away and actually studying a completely new organism right now?
Yeah, here’s how I would phrase it. I would say that the most important thing you have to have is a biological question. If your biological question can be addressed by yeast, go for it. Go do yeast. Now, there are thousands of species of yeast, so you could take advantage of that later, but go for it.
But, if your question is ill-suited to the systems that have already been established, it might be appropriate for you to walk away from the path and start prospecting for species that may be exaggerating the attributes that you need in order to address the question that you’re most interested in, right?
And so that is the problem as I see it. Is that I think that a lot of people are asking the same question. They’re not asking as many questions as there are there to be asked. I hear with frequency when I used to visit the universities before the pandemic, that the students would tell me, “Well, you know, but I think all the big questions have been asked. There are no big problems to solve.”
I worry when I hear that from a student, I mean tremendously worried. You know, it’s like an apocryphal story of the Congress wanting to close the Patent Office because everything that has been invented has been invented already. I mean, it’s the same logic. That suggests, essentially, that, you know, we are, we have no longer an imagination and that everything that needs to be understood is understood.
Then it’s appropriate to take a step back and ask yourself, “Do we really understand everything? Is it true that, you know, all of this information that is being recorded in these dozens of journals, does that really help us understand the things in the natural world that we don’t understand?” And you can ask yourself some basic and fundamental questions: Is this an appropriate processes?
It’s an inductive inquiry process–not so much a reductionistic process, but an inductive inquiry process–which is, do we really know, okay, how an embryo gastrulates? So you go down the list and you read Ray Keller’s papers and all the people’s papers. And then you say, “Okay, well you have a really good understanding of how gastrulation takes place. Okay, well what about scale and proportion? Because, you know, the blastopore lip is usually of a particular size in relation to the size of the whole embryo. How is that determined?
That’s right– tumbleweeds and crickets, right? So why, okay, so is Xenopus the best amphibian to study this? Would salamanders be the best amphibian to do this? Or is there another amphibian out there that actually breaks these rules, where the blastopore lip is as huge as the embryo?
My suspicion is from just, you know, a preemptory screen of nature is that if there are rules, they are being violated already by natural experimentation. There is probably going to be a system out there that did not get the memo that they needed to follow these particular rules and therefore, you know, abide by them.
And that’s how you begin to identify, you know, lacuna in research systems that you can try to fill in by identifying other organisms. You don’t have to be exotic. They don’t necessarily have to be exotic, they just have to be the right species that exaggerates a particular attribute such that you can go in with the tools that we have today and then transform that system into a bonafide, vulnerable to experimentation, molecularly accessible research organism.
This was not possible 10, 15, 20 years ago. This is possible today and so this needs to happen and I think we’re not encouraging our trainees to think in this particular way. Like I said, you know, if you’re interested in Wnt signaling and Wnt signaling, you want to understand it in mammals, we have systems for that. But if you want to understand, you know, why is Wnt signaling as diverse and as powerful and as pleiotropic as it is?
It may be that, you know, that one system will not fit the bill and that you will have to look at other biological contexts in order for those contexts to inform your thinking about that pathway. At that point I would say, well, maybe you want to go beyond Drosophila, maybe you want to go beyond mice, maybe you want to go into a biological system that is in a particular context that is not really experienced by these other model systems that you’re studying.
And now ask your question: How has environmental change affected the expression and the power and pleiotropy of the signaling pathway?
If you have a particular biological question you’re interested in and you’re pretty sure some other organism is going to be the best way to do it, what are the approaches you’d take to finding, you know, the organism? You described actually looking at each organism for which ones regenerated. Are there resources out there? How would you approach it at this point in time?
Yeah, well, at this point in time, you know, I wish I had Google when I started looking at it. Because I have to tell you, I spent a significant amount of time in libraries. I spent a significant amount of time in the MBL library, in the Library of Congress in D.C., in the Smithsonian library, just looking at a variety of sources of information.
Now, with Google and with, you know, search engines for literature and the like available, that is really a good place to start. It’s just looking at what’s out there. Now it’s still incomplete. It’s still incomplete, but I would say that if you have identified a problem and let’s say that you know that this problem is manifested in a particular species of interest, there is probably going to be a review written for that particular species. It might be mouse, if it’s a comprehensive review, that will list some examples, okay, of organisms that do this that we don’t understand what that is.
I will go back to that primary literature and then start digging and digging and digging and digging and digging. In the process of doing this, you’re going to find other things that were not intended for it to be part of the, of the actual first citation. And so one of the things I would encourage you to do, which is something that we, because of the exigencies of the time, on us trying to keep up with the newest and most recent literature, is that when you have a problem that really, really wakes you up at night and you think that this is something that cannot be addressed with any of these available systems, you need to read with abandon in a completely undisciplined fashion.
I know this sounds counterintuitive, but you need to read with abandon because what’s going to happen is you’re going to start learning about certain aspects of that particular landscape of investigation and scholarship that somehow contains your question and it will actually lead you some growth that you would not find otherwise.
This is where Google will fail you. Google will not take you there but if you read with abandon and you start reading about, let’s say for example, I’ll give you one of my, a recent example. I was actually very interested in understanding, you know, how did we get into, like, marine systems, or how do we get to see like, you know, things that were living in water because aquaria had not, they were not available. I don’t remember reading a single medieval story of an aquarium with a fish swimming in a vessel.
I don’t remember thinking about, you know, people keeping fish tanks. So, this is a fairly recent invention. Aquaria, you know, glass vessels to put animals in them. We used them to drink stuff from it or to bathe in it. But we never put animals to observe them.
So, that led me to the eventual discovery of a woman scientist in France whose name is sketchy at the present time. I can’t pronounce, my French is terrible, but what she actually was able to do was to actually collect jellyfish, which were impossible to investigate out of water because they’re formless. They need water, is the skeleton of the jellyfish. It’s what keeps their shape. So as soon as you put them out on the net, they just look like this gelatinous blob that, you know, is completely difficult to analyze.
So she came up with this brilliant idea “What if I put them in a bucket, but I make that bucket translucent? I’ll make it out of glass.” And so she was the first person to come up with this, puts it in there, and recorded for the first time the lifecycle of a Mediterranean jellyfish, which had never been described before.
Now I would have never found this in Google and the reason why I was thinking about this is because I’m thinking of ways in which we can, really, you know, establish a type of benthic or pelagic environment where we can collect animals close to the ocean, for example, and keep them in as natural an environment as possible, as opposed to asking us, to the animals, “Adapt to my conditions,” which is what we’ve done for bacteria, yeast, mice, Drosophila, C.elegans. We’ve asked all these species, “Adapt to us, and now we can ask you questions.” I want to flip that around and I want say like, “Can we adapt to you and then, you can give us answers.” And then, you know, so that’s what I mean. So you do need to, you know, just read broadly, think broadly and follow that thread wherever it leads you.
At the end of the day, it’s super rewarding because you learn a bunch of new stuff and you never know whether the new stuff is actually going to help you see things in your own experiments you had not considered before. So that is how I would do it, just take full advantage of the many, many tools that are available to you today. It’s remarkable what we have available today.
That’s a good segue into a few of the other questions. So, a number people are wondering what about collaborating with, you know, ecologists or wildlife biologists, is that something that you’ve done and you would recommend for someone who’s thinking of moving in this direction?
Yes, I mean, I think that is a fantastic question. It’s something that I have not done and I feel bad about it because it is impossible for a biologist to claim that they understand a biological system if they don’t understand the environment that chiseled that excellent species into what it is today. It’s really difficult to imagine that population dynamics, you know, trophic cascades, changes in temperature and salinity, the kinds of things that normally happen, and on a regular, you know, day of the week, did not have a role on the biology of trying to understand.
So, that’s what I mean by saying that it’s time for the modern life scientists to bring the lab into nature and not the other way around. So I think it’s super important. I mean, I think, for example, my field, I think is very close to developmental biology. I think the developmental biology has a lot to contribute to climate change, has a lot to contribute to coral bleaching, has a lot to contribute to a large number of global biological processes that developmental biology has not studied because it has focused primarily on animals that are being brought into the lab.
So guaranteed, for example, that any of these, you know, larval stages of many of these marine species that are in a water column that really is going to depend on salinity of the water, because that will define buoyancy. It will depend on temperature because that will determine how quickly or how slowly certain molecules are going to execute their enzymatic activities. It’s also going to depend on how much light is there, because some of these processes will require light and water is a blue filter, so probably not just any light, but it’s very specific wavelengths of light, right?
And so we have no idea how those factors may have played in, you know, the evolution of Nematostella, which is an emerging research organism that now is being used to understand the origins of multicellularity. But I’ll guarantee that this works. It has worked in chiseling at biology simply because, you know, we know where they live. And so, you know, in the mornings, the water is cold. They are close to the littoral, they’re close to the coast. If they’re trapped in a little puddle of water, as the temperature rises and it’s completely uncovered, the salinity is going to go up and it’s fine. This is all part of that process of adaptation and we know very little about it.
What we do know is that we bring them and we put them into a country club–constant food, constant temperature. You know, all of the best conditions. Little, you know, bacterial infection, little competition. And then we hope that that’s going to tell us something about the organisms. So, I think it’s very important, going forward, for all of our disciplines–cell biology, developmental biology, stem cell biology–to start thinking about where do these biological activities, where do these cells come from?
They came from nature and nature is a combination of ecology, population dynamics, you know, climate. There’s all kinds of factors that we just simply don’t add to our equation. So I think it will be very important for, you know, the new generation of life scientists to start thinking much more broadly about what that biology they’re trying to understand really means.
And the reason why I think it’s important is because, you know, that may actually be much more helpful in identifying the causes of cancer then actually looking at cancer in cells that are already sick, right? And so, there is a reason why cancer exists and is probably going to be found in a natural environment, under natural conditions that made those cells, you know, if not competent, at least vulnerable to produce this type of cellular activity and we are completely ignorant, in my opinion, of those particular processes.
Stephanie had a question which was sociological in nature that I thought was interesting. She says, “For someone who is looking to branch into non-model organisms, how do you find quote-unquote your people? It’s hard to find appropriate conferences and communities because you often have to choose from the ones that are studying the pathway you’re interested in and whatever model organism was used. Or the organism you’re interested in, where people may not be as familiar with, you know, your particular way of doing science, or that could be any ecological or, you know, population biology community. What are your thoughts on how to create the kind of communities that the traditional model organism have created for supporting young researchers?
Yeah that’s a really, really good question.
So, the issue with the so-called model organisms is that, you know, since they arose organically, you know, there was one particular lab that began to train other people, then those people went on to make more labs of that particular system, for these yeast or Drosophila and the like. That grew up organically into a community.
That’s very difficult to emulate, when instead of one organism you’re talking about, say, a dozen of them. So, you probably have twelve different people working on twelve different systems and it may not be that there’s a critical mass to generate a organism specific, you know, community, right?
So, the alternative to that is that instead of focusing on the organism, you focus on the biological problem. And so if you want to identify members of your tribe in, you know, in the kind of problem that you’re interested for that particular organism, I would suggest that you participate in meetings such as the Society for Developmental Biology annual meeting, and the regional meetings are really good place to look for members of your tribe. And larger meetings like the American Society for Cell Biology, as well. And the reason for saying this is that more often than not, there will always be a session, or a number of sessions, where the platform speakers or a poster, or poster sessions where there will be a highlight on so called, you know, non-model organisms, which by the way, this is a terminology that I despise because every organism is a model of something.
It’s just that we’re not asking the right questions. So that’s part of the sociological thing, so there may be these, like, research organisms there are non-traditional research organisms, the ones that the ones I’d like to call the UN Security Council of Research Organisms, right? And so that’s a practical way of doing so. And then once you identify members of your tribe, there are many ways in which these communities can stay together, which is very difficult before. I mean, social media is a fantastic place to gather and convene this exchange of information.
I know that there are people, for example, on Twitter that are working on Platynereis or are working on strange, you know, echinoderms or other types of benthic organisms. You can actually bring all of those individuals into a group and start corresponding with them and start generating a community that way. That may ultimately transform into a physical community that you can actually organize meetings and interact with, or, alternatively, in this day and age now where everybody’s a Zoom expert, you could begin to convene your own meetings. I mean, there’d be no reason why you could not do that, assuming that you can come up with an agenda and a series of exchange ideas that will allow you to coalesce these individual members around. So, it requires a little bit of legwork, but it’s something that I know that other people are also on the lookout and it’s just a matter of time before those individuals collide with each other and begin to produce interesting interactions between each other.
Yes, so maybe we need to build additional organizations that would support broadly people working in, you know, non-traditional and new organisms.
Yeah.
Probably you can’t have a society of every new organism, right?
No, but, you know, it should be possible, right, I mean I think these would be incredibly interesting meetings because there would be a situation where people working on a specific biological problem will actually come and look at a new biological context in which to try to test this idea. You see this very often at places like the MBL, right, when people who have been working on mice all of their lives all of the sudden discover that well, hydra has, you know, nerve net that, you know, it’s as simple as nervous system as they can possibly imagine. And so, now they start looking at these new biological contexts and ask the questions they were trying to dissect in the complex cortex of the mammalian brain.
Raphael Yuste is a really good example of this, you know, dedicating his life to neuroscience, working primarily with mammals, and now he, in his late life, has discovered hydra, and it’s provided him with a new, completely different perspective of how to understand neuronal interconnectivity. It all required, it only required, was a change of biological context and I think it’s something we just under appreciate and we’re not really taking full advantage of.
That’s great. A couple of very concrete kind of grant-strategy questions have come up. A number of people want to know, you’re moving into a new organism, how do you convince reviewers that you have the expertise necessary? That’s often a common criticism one hears.
Yeah, that’s true. That’s a criticism. So, I would say that just focus on the technology, right? I mean, what I would say is that you have a really important biological question you want to address, here’s the system you want to address it with and, you know, RNA and DNA are RNA and DNA. So, in all likelihood, you’re going to have to define, you know, transcriptional profiles, or you’re going to have to define genomic composition, or if it’s a little bit more advanced system, you might have to define, you know, chromatin immunoprecipitation protocols, what-have-you. I would focus the grant on providing the reviewer with the appreciation that you have the technological know-how to make the system yield its valuable information.
I never worked on planarians when I wrote my first planarian grant. I mean, I’d seen pictures of it, and then I thought like, well, it might be appropriate for me to order a couple from Carolina Biological Supply while I’m writing this grant, but what I learned from this experience was that even though the reviewers commented that I had no experience working with this animal, that there was no track record, I didn’t train in planarians as opposed to, this was completely out of the blue. They were, their confidence was buoyed by the fact that the molecular approaches that were being proposed to dissect this problem would be the molecular approaches that they felt most confident would provide with the most information.
So I spent a huge amount of time making sure that the technology that goes along to address the biological questions had the sufficient, you know, rigor and the sufficient density of substance to make the reviewers blink and say, “Well, I’d be curious to see what this turns into.” So that’s one way that, at least in my experience, has helped me, you know, overcome the lack of experience and familiarity with the system. Because that’s a slippery road.
I mean, there are people who work on a particular system that dedicated their lives to it, their lives to, right? It’s really difficult to imagine that in the span of three months, you’re going to become that person. That’s not possible, but that person became an expert in that organism because that’s all that person wanted to do. But is that person a specialist in that system because they were asking a very specific biological question? It more often than not, that is not the case.
Let’s think about Sydney Brenner. Was Sydney Brenner a nematologist? No, he wasn’t. What he brought to nematodes was genetics, and he identified a vulnerability in the system, which was that they were transparent. But I don’t think he had, he had never heard of nematodes before he started working on them. So, I think that’s worked for him and that’s worked for a lot of other people that have began to, you know, foray into different systems is that the technology is the big opening for you to be able to make your reviewers blink and give you the benefit of the doubt.
That’s great. So a couple of questions about technology. So, you know, in this age where we have CRISPR, as you mentioned, and, you know, sequencing techniques that have really opened up the space of biology we can discover, are there technologies that you see as missing that, you know, would really revolutionize our ability if we had them, an opportunity for a young technology developer to come in and really change the world?
Yeah, I think there are many deficiencies in our ability to actually not just observe but manipulate temporal transformations of any kind. You know, when you look at a single cell paper, it’s a snapshot. It’s just a bunch of cells that got destroyed in that moment in time and you’re trying to extract all kinds of dynamics from it. That might be looked at, you know, 10, 15 years from now as medieval.
It’s really just, even though it’s like the apogee of technology today, right? So, I would say that any technologies that allow us to measure, unperturbed, in real- time temporal transformations in sufficient numbers so that we can extract valuable information from it would be extremely, extremely useful in allowing us to make the next conceptual leap in our understanding of biology. One thing that is very clear to us in biology, and drives physicists crazy and mathematicians crazy, is that ours is a discipline of statistical measurements, right, because no animal is exactly the same. You know, it’s not like you can comment, it’s not going to be the same muon, it’s not going to be the same lepton. I mean, no.
The animals are different even within a population. That’s why biology is so beautiful. It’s because of this inherent capacity to not remain constant. If it were constant there would be no evolution and, therefore, we wouldn’t be talking here right now. I mean, you know, we’d be just bacteria, what have you, there’s no way to change. But those changes, as they occur in real time within a species, are the changes that ultimately will result in speciation. If we could visualize those process, or some aspects of those processes, that would give us the next conceptual leap, I think, in our understanding of biological processes.
And, again, the statistics will come into the picture, so I would love to see an emerging, you know, new discipline of, you know, statistical developmental biology or statistical cell biology. Where we’re no longer looking at just one or two images because they are so difficult to collect, but thousands of them and they know really how many degrees of freedom does this particular biological phenomenon actually has. Because that will tell you how amenable it will be to a transformation, to make that leap from being, you know, aquatic to terrestrial, for example, just to exaggerate. Those are the particular biological attributes in which evolution is going to have the most abundant playground, or fields for a playground, than ones that are very, very rigid, I mean.
And so anything that allows us to visualize this will be terrific. Imagine for example, just to conclude, if you could actually visualize, you know, modifications of histone tails in real time as the cells are making decisions on how to interpret external signals and what genes to turn on and what genes to turn off, globally. Imagine if we could see that in real time as opposed to having to grind the cells and do a chromatin immunoprecipitation. I mean that I think would be super transformative. And it sounds like science fiction today but I tell you, single-cell sequencing sounded like science fiction to me just three years ago. So it is possible. If it doesn’t violate the rules of physics, it should be possible to do.
I like that. It’s a great way to end. Thank you so much, Alejandro, this has been a ton of fun.
Thank you, Jon.
As always, you’re very inspiring and keep doing what you’re doing. I’ll just say to the trainees joining us: First of all, I hope you were as inspired as I was by this presentation from Alejandro. NIGMS is very interested in this kind of work and seeing people move out of the lamplight, as I say sometimes, into the darker areas of biology. Success rates for early-stage investigators last fiscal year were about 40 percent, so that’s pretty amazing. And I think, you know, there really is space for you to go in these new directions that Alejandro so eloquently outlined for you. So, Alejandro, thank you again. This was a lot of fun.
Thank you very much, Jon, and everybody at NIGMS for the great work that you guys are doing. We greatly appreciate it. Thank you.
And thanks to all of you out there who are either staying home and staying safe or are directly contributing to, you know, trying to respond to this crisis that we’re in now. Thanks everybody.
