KARIM LAKHANI: So tell us what Flagship does?
NOUBAR AFEYAN: Yeah.
So Flagship is first and foremost a life science innovation company.
We have our own way by which we innovate, which I'll tell you about.
Once we come up with something that's worth taking forward,
we form a company to take that forward.
And so we also have to figure out how to do
venture creation in a systematic way.
We have our own capital that we deploy into these companies
to help them grow for the first two, three years.
So up until then they operate as wholly owned pieces of Flagship.
And then we spin them out.
And we spin them out, and for the first time, additional capital comes in.
But by that time, the culture, the senior leadership team,
the early proof of concept, the early kind of customer or partner traction
is there.
And it looks like a company ready to eventually live its life on its own.
So we're not interested in building kind of subsidiaries, open-endedly.
Every single thing we do ends up becoming a company or nothing.
So we've become kind of a creator of companies around internal innovations.
Now sometimes these innovations draw from external science.
And I can describe that.
But we're not only trying to find science and then find what
to do with it and create companies.
That's become in vogue for the last few years.
We've been doing this for 18 years.
But we've ended up in a place where we think the sustainable
way to do this is to have your own innovation capacity, your own company
creation capacity, initial growth, and then the companies have the wherewithal
to grow and compete and thrive.
KARIM LAKHANI: That's fascinating.
So walk us through one example of a company
that you guys have given birth to from the start
to it's leaving the Flagship fold.
NOUBAR AFEYAN: There are many.
I think we've been involved in doing about 50
of these that are based on internally developed science.
And there's a whole bunch more that also include external.
But I'd say one of the internally developed ones
that just recently went public, I can give as an example is Moderna.
So Moderna was-- and I'll tell you.
We have this fairly, let's say, prescribed process.
Which the way people think about entrepreneurship and innovation,
especially breakthrough innovation, is that it is unruly.
It is chaotic.
It is inspired.
KARIM LAKHANI: Serendipity!
NOUBAR AFEYAN: In my view, it's none of those things.
KARIM LAKHANI: None of those?
NOUBAR AFEYAN: Absolutely none of those things.
I have a completely contrarian view of that.
And I've done it enough times in enough different fields
that I think, frankly, just to be a little controversial,
I think that's an illusion.
In other words, I think that because people haven't done that thing before,
it's exciting and unexpected to them.
But actually, pretty quickly, it looks like just another version
of what came before them.
Because the historians come and say, well, you know,
before there was the iPad, there was the iPod.
And before that, there was the Walkman, et cetera.
And also, when you look at it that way, you go, well, why were you surprised?
And that's when you realize that these things are just evolving.
And I'll give you an example in this company called Moderna.
But before that, I'll tell you that underlying
how we think you can do this systematically
is the notion that breakthroughs aren't made by people.
They emerge.
And the most understood, not well understood,
but understood version of emergence that we know about is evolution.
Which is that if you do variation, iteration, selection
and iteration systematically, the winners will emerge.
And when they do, they will look surprising.
But actually, they're the result of that process.
They're not some inspired thought that has nothing to do with that process.
So hold that thought as I give examples.
They'll all be examples of that.
And that actually does cause one to think differently
about being possessive about all these companies and all these innovations.
We're not.
We don't go around saying we invented this.
We may file a patent and get an invention.
But where these ideas come from are very emergent.
So in Moderna's case, talking about emergence,
we understood by following the various scientific advances
that people were playing around with converting fibroblast cells into what's
called induced pluripotent stem cells.
Somebody won a Nobel Prize recently for this.
These are called Yamanaka factor.
So it turns out that if you take differentiated cells,
and you introduce a couple, three different proteins, four of them
specifically, these cells can de-differentiate and look
like what came before them, stem cells.
They're not normal stem cells.
But they're close to being stem cells.
And so why do that?
Because then you could differentiate it and make other cells.
So that was the general field.
And in that field, there have been some people, particularly at UPenn and then,
more recently, at Children's Hospital here
in Boston, who had been playing around with using what's
called mRNA, messenger RNA, to use these to go into cells
and express these proteins.
Why had they done that?
Because it turns out this mRNA, they could actually
get a better transformation of these cells.
And so we were aware of this work.
And we started asking kind of just what if questions.
KARIM LAKHANI: So your team is reading scientific papers.
It's in the air.
NOUBAR AFEYAN: In this case, yeah, exactly.
And we do this all the time.
And basically, we're--
KARIM LAKHANI: You're in the midst of this flow of knowledge being used.
NOUBAR AFEYAN: It's not about reading papers for us as much as just, I mean,
we are talking to lots of people about lots of different things.
Or somebody says, hey, by the way, you know, I just saw this data.
And then we actually read papers in hindsight.
In other words, we read papers once we have an idea of what to do,
as opposed to read papers to get an idea per se.
The signal to noise in papers is gigantic.
If you sit there and read 1,000 papers, and that
gives you three ideas, hard to do anything else.
So I'm sure that can be done, too.
But that's not the way we approach it.
Anyway, so long story short, we started wondering, for lots of reasons
that I can't almost reproduce because you'd have to go back to 2010
in the summer and whatever else was being thought of at the time.
So understand, by that time, we had about 20 people
that were doing this type of activity in various combinations for a living.
And so it's important.
Because these ideas kind of get mixed and moved around.
This is not-- one person thinking deeply is not going to get there.
So we start asking, can you think about--
we said why is there no drug that is based on mRNA?
Now if you go back 10 years, drugs were made out
of proteins and small molecules.
There had been an effort to use viruses to introduce genes
into the body called gene therapy.
And a person had died early on and that whole field was shut down.
And there really was no other variation to proteins or small molecules.
And there've been some efforts to try to make, not to get too detailed,
but other small DNA, RNA molecules, antisense, what's called.
And we were aware of all this.
But we're thinking, why don't people actually use this microRNA molecule?
And that's just a thought experiment.
And you can go and answer that question.
KARIM LAKHANI: So you raised the problem?
NOUBAR AFEYAN: You raise--
you don't say, you know, initially, we don't start with,
we need to cure melanoma.
We don't start it from what good is this mRNA that can transform cells.
Because it's not good for anything other than that.
But we just kind of abstract it and said,
is there a combination of a solution and a problem
that we can identify simultaneously around this space?
And if there isn't one, then we move on.
And in this case, that's part of our methodology.
In this case, what we concluded was that people had tried and failed
10 years earlier.
We understood why they tried and failed.
We realized that there was no obvious fix to it.
But there was a direction of fixing that you could modify chemically
some of these RNA molecules.
And they at least hinted that if you kept doing that,
there may be better ways.
We had no proof.
There was no academic literature that said this can be done.
Now we could have waited for that.
But we probably would have been five, six years.
Because now, there is academic papers from which
we could have started companies.
But our whole thing is to almost mine this science of the future
to try to solve problems of today versus mine the science of today
to solve problems of the future.
And that is exactly backwards.
And it's not any better.
It's just that you look at the world differently.
So publications give you evidence for what you want to do.
But that's not why they publish those things.
They were thinking of a very different thing.
You know what I'm saying?
So in that regard, that's a little bit.
So in Moderna's case, we identified--
well, the other thing that we do, a very integral part of what we do
is that we don't do this in a vacuum.
So we go out and talk to people about our hypotheses.
These are not--
KARIM LAKHANI: You're not afraid of people taking your ideas?
NOUBAR AFEYAN: No.
And I'll tell you why.
So we use, in order to try to create an evolution-- so we're trying
to create an evolutionary environment.
How do you do that?
The scientific method uses hypotheses and experimentation.
So we actually do the same thing.
We create value hypotheses.
We basically say, I will take an mRNA molecule, formulate it with this agent,
stick it into muscle.
Use muscle-- none of it is true.
None of it's been done before.
But it's just a starting point.
We then go with that to a handful of folks
that are both experts and nonexperts in the field, super important thing
if you're going to practice this kind of work
is that experts actually are not the people who
are going to give you an idea of how to do things dramatically differently,
because they became experts by already doing something
dramatically differently.
And now they're defending their territory.
So if you go to talk to somebody and say, can this be done out here?
Most people we talk to, they can tell you precisely why it can't be done,
which is really valuable from a selection pressure standpoint.
But not the source of kind of-- and here is a completely different way.
So other people, though, who don't have expertise,
but have interesting creativity-- so what we do is we take our hypotheses,
and it's never one.
Because one of the things we've learned is
that if you start with one starting point,
you only locally search the space around it.
So we sample multiple different points.
So it might be how about mRNA as a way to make more proteins in a fermenter?
So around the theme, we come up with totally different variables
we try to identify.
And then we put a starting point.
And then we start talking.
And then what's been interesting and a great learning exercise over the years
that we've seen is that if you go to somebody with a bad idea,
but you actually present it in a precise way,
they will tell you why it's a bad idea.
And in that transaction, something happens.
They feel smarter.
KARIM LAKHANI: Yes.
NOUBAR AFEYAN: And you get selection pressure.
And so the way our process works is that we actually
do this with multiple people.
So when you said, aren't you afraid they're going to take your idea?
What are they taking?
We just made it up.
There's zero fact to it, literally zero fact.
KARIM LAKHANI: Just imagining a hypothesis?
NOUBAR AFEYAN: Exactly.
We're just a hypothesis.
And they know it.
Because then they tell us, what proof do you have?
I say none.
So then, they still engage.
Because when we talk to these folks, and this is what we're known for,
we create a bit of an expert-free zone in the sense that-- you see, look.
These scientists and here we are at Harvard and MIT, Stanford,
these people go to the meetings of their fields.
And they cannot say something that does not seem unbelievably smart
and reasonable.
Actually, I'll make the point.
Let me caveat.
Reasonableness, in my view, is like the gravitational force
that keeps innovation from happening.
Because people enforce reasonableness in the scientific world
on what you are allowed to say.
You go publish something in the literature that's
not reasonable to the reviewers, you can't publish.
KARIM LAKHANI: You're killed.
I've done a whole study on that.
NOUBAR AFEYAN: Right.
So ask yourself the question, why is it that we
think that the only innovations worth working on start their life reasonably?
In fact, I can show you many innovations that are now,
you know, accepted as real, transformative things.
Every one of them started life unreasonably.
And yet, we go look for them in reasonable places
by reasonable people who are using reasonableness filters to kill them.
So because we knew that, this was not the first thing I had done,
we kind of say, look, let's just forget reasonableness for a second.
Just think with us.
And they tell us bad idea.
Somebody in Japan had tried it.
The experiment won't work.
And we keep tweaking and tweaking and tweaking.
This is different than you hear a lot in Silicon Valley
speak, kind of a pivoting.
This is not pivoting.
Evolution is the master pivot.
It's, like, nonstop pivoting.
There's nothing to pivot from and to.
You're just adapting and surviving.
So that mindset is super important.
Now what happens is, over time, things emerge.
Or they don't.
But they emerge where the next person you talk to,
they can't find fault with it.
You know that because it frustrates them.
And then they start telling you, well, do you have any proof?
You go, no, no, no.
I just made this up.
It's just that we've been-- anyway.
And then that point is when we go into a lab for the first time.
And then and only then do we test the idea.
Now you can't test it fully.
You can't test it, because it takes years and years.
And one of the expertise we've developed over the years
is how to figure out what to test first.
And in life science, you can't use these words, killer experiment.
Because you know, life sciences, kill.
But you want to do the killer experiment early.
And so figuring out what's the killer experiment, or two or three or four,
that if it doesn't fail allows you to go forward, that's the trick.
And we do that in our shops.
And in Moderna's case, we spent a couple of million dollars,
about six months doing a set of key things
but for which we would not have proceeded.
So we knew the idea had morphed and evolved and had some resilience to it.
We went into labs and asked specific questions.
Once we saw that actually some of the things we were hypothesizing
could be done partially, we then decided, OK.
Let's form the best economic value creation
engine known to mankind, which is a startup in my view.
I'm biased.
And then we deploy that startup to go after that value pool
in as many different ways as we can.