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
Download Recording [MP3]
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
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
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
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
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
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
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
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
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
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
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
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
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
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
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
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,
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
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
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.
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