6 | Harmit Malik’s dark alleys to discovery

In this episode, Itai and Martin talk to Harmit Malik, Professor at the Fred Hutchinson Cancer Research Center and President of the Society for Molecular Biology and Evolution. Harmit’s main Night Science tool is to talk again and again about the same puzzling observation to different people, drawing variations of the same story on the blackboard. At some point, he says, you realize that something in your story never changes - that is  where the false assumptions are. Harmit thinks that in pretty much every important result he published, there was a point where he thought the project had failed – where a major result contradicted the original expectations. But that “failure” actually points to the dark alleys where the true discoveries hide. 

Harmit studied Chemical Engineering at IIT Bombay. Today he studies the causes and consequences of genetic conflicts that take place between different genomes or even between components of the same genome. His main interest is in fast-evolving genes, trying to understand molecular “arms races" and how they drive genetic innovation. Harmit is a member of the US National Academy of Sciences.

For more information on Night Science, visit www.night-science.org .

Chapters

• 0:00 Introduction
• 2:06 Creative requirements of being a scientist
• 9:01 Breakthroughs start as contradictions
• 20:46 Challenge every assumption
• 30:57 Making time for night science
• 35:51 Supporting failure nurtures innovation

Transcript

Harmit: So, when you're just telling yourself the same thing over and over, you begin to sort of question each step or each assumption that you made.

Harmit: And often that process, where you sort of doodle, I actually take pictures of these chalkboard things, where I, you know, after I've drawn something out, I'll take a picture, and suddenly I have these cascading slides of multiple models that I've built.

Harmit: And certain models, you realize you're making the same model over and over for the same part.

Harmit: And then you recognize that that's probably the place where you're making the false assumption.

Harmit: Because, you know, the thing that you've not challenged is probably where the flaw lies.

Harmit: And I would say that 90% of the time, that's turned out to be true.

Martin: Welcome to the Night Science Podcast.

Itai: Where we explore the untold story of the scientific creative process.

Martin: We are your hosts.

Itai: I'm Itai Yanai.

Martin: And I am Martin Lercher.

Martin: Welcome to another episode of the Night Science Podcast.

Martin: And today with us, we have Harmit Malik.

Martin: Harmit got his bachelor's degree in chemical engineering from the Indian Institute of Technology in Mumbai, India.

Martin: And today he's a professor and associate director of basic sciences at the Fred Hutchinson Cancer Research Center, the Hutch.

Martin: And he's also an investigator at the Howard Hughes Medical Institute.

Itai: And Harmit studies the causes and consequences of genetic conflicts that take place between the different genomes or even between the components of the same genome.

Itai: He's interested in understanding these molecular arms races and how they drive genetic innovation.

Itai: Very impressively, Harmit has been recently elected to the US National Academy of Sciences.

Itai: And Harmit, it's so great that you are with us.

Itai: Welcome.

Harmit: It's a pleasure to be here.

Harmit: Looking forward to this.

Itai: So just to get started, we're wondering if we can ask you a very broad question.

Itai: What does it take to be a scientist leading a lab?

Itai: And what we mean is what are those creative requirements?

Harmit: I think people have different definitions of what it means to be really successful.

Harmit: I think some people choose to believe that that is really about the enterprise, about making sure that the lab is, you know, almost like a small business, it's well funded, it's successful, et cetera.

Harmit: I sort of choose to believe that a lab is successful if it's making really creative inroads, perhaps into areas that other people are not looking at.

Harmit: You know, being a geneticist by training, something that was really ingrained in me was the value of trying to pass the deletion test, if you will.

Harmit: You often are in areas that will allow you to make original insights, and deliberately trying to be in those areas is something that we strive for in the lab.

Itai: What do you mean by deletion test?

Harmit: If you look backwards in time, we have the pleasure of hindsight here and the benefit to look back.

Harmit: You can see that even in fields that are now extremely well populated, a lot of the fields started off with observations that were made often in a number of labs, a few labs in the beginning, where they went off and often spent years, often decades, kind of working on a particular aspect of biology that was not super fashionable at the time.

Harmit: And then when it worked, then it was a little bit like a gold rush.

Harmit: And sometimes in the midst of the gold rush, it's hard to really pay attention to the people who did really a lot of the foundational work.

Harmit: In my own field where we sort of focus on, for example, heterochromatin biology, or even things like polycomb, there were years and decades of work where people were focused on just understanding polycomb for its own sake.

Harmit: And now, of course, it's one of those very, very fashionable items.

Harmit: And so the question is you can sort of either be very successful by identifying really great opportunities for your lab in which you can actually make an impact, or you can choose to identify opportunities where others aren't seeing quite the opportunities, but you're really convinced that there is something really interesting going on biologically.

Martin: So from your own personal experience of developing as a scientist, do you think that there is a set of steps that you have to go through in that development?

Martin: In other words, do you first have to learn how to answer questions and then how to pose new questions yourself, or is there maybe any other order of how things develop?

Harmit: I think one of the things that was really special about growing up, if you will, in a small department of biology that had both molecular and cellular biologists, as well as ecology and evolutionary biologists, is that we did get well trained in the mechanics of doing science, but we actually spent a lot of time in journal clubs dissecting how people kind of chose problems and what was the hurdles that they would have had to overcome in order to really make their original insights.

Harmit: And I didn't really realize until much later how much of a profound impact this sort of experience of dissecting really fantastic scientists and their original insights really had on me, where not only just were taught about how to do science, but actually how to think about science, how to choose problems in a deliberate fashion.

Harmit: And I wouldn't necessarily say that we were expressly coached in that way, but just hearing these examples over and over from completely different fields, that was definitely transformative and definitely had an impact in what we chose to do in our own labs as we developed as scientists.

Martin: I'm a little bit surprised because usually the way that the development of a project is described on journal pages is very different from how it happened in reality.

Martin: Usually you don't really get an insight of how people first stumbled upon the problem and how they first try to solve that.

Martin: You only get the finished polished product.

Harmit: It is definitely true that what we hear is really the polished post-production view of how the science was done.

Harmit: But actually if you even go back to the papers that were published in the s and s, that was not the case.

Harmit: Actually people were pretty free form in terms of how they thought about their things, what connections they made.

Harmit: And they were actually pretty brave and basically completely admitting how this was not necessarily a perfectly founded idea.

Harmit: Then often the motivation for the science was simply like a curious observation that they made, often completely by serendipity.

Harmit: And they were completely brave about admitting it.

Harmit: Now these are not things that we would actually now see in the pages of Cell, Nature and Science, because everything is extremely polished in a post-production world.

Harmit: But it was really influential to see.

Harmit: And then the other thing that was really great as a graduate student is that we got to actually meet some of these scientists, especially in the evolutionary world, where we brought them in for seminars.

Harmit: And then the graduate students and post-docs had an opportunity to kind of hang out with them and ask them questions about like, why would they choose to do that?

Harmit: Or what were the steps that they did?

Harmit: And actually not just learning the finished product, which we had already read in Journal Club, but sort of figuring out how the sausage was made, so to speak, that was really influential.

Harmit: What you really deeply appreciate is you have these creative insights that really come from nowhere, but often just come from the ability to connect things that people in disparate fields have already seen and taken for granted, but then you really realize the connection and you're in this unique place because you are perhaps one of the few people in the world who's recognized that connection.

Harmit: I distinctly remember a fantastic visit by somebody whom I deeply admire, whose name is Bill Rice.

Harmit: He is an evolutionary biologist at University of California, Santa Barbara, and he had really published this series of brilliant experiments in which he had really arrested the evolution of Drosophila male flies and shown that when you do that, you can actually in the laboratory observe evolution and action in terms of sexual antagonism.

Harmit: And he was pretty honest about the false starts, right?

Harmit: Like the other thing that we don't see in papers is well, was this the first thing you did or was this like the third thing you did?

Harmit: Because the first two things you tried really didn't work.

Harmit: And that was actually really influential to hear his false attempts.

Harmit: And then having already recognized his successful attempt, we really got the perspective on what it took to really be brave in this new arena of science and how he was ultimately really successful in establishing a new paradigm.

Itai: I wanted to ask you, this is kind of our main question, one that Martin and I spent a lot of time thinking about in our Night Science discussions.

Itai: Do you have a process that you would call your creative method?

Itai: In other words, is there some specific habit or technique that you use when you try to come up with some thoughts about a particular puzzling observation?

Harmit: I'll give you an example from work that we are actually currently working on.

Harmit: My lab is very interested in rapid evolution.

Harmit: And so a lot of the project ideas in the lab really stem from an observation of rapid evolution in genes or gene categories, where we traditionally do not expect to see rapid evolution.

Harmit: When we think about the cell, we tend to think about it as this Swiss watch-like analogy, where there's a lot of interlocking gears and the cogs really need to work with each other.

Harmit: So we can't really afford a lot of rapid evolution on any one of these because there's a real risk that you will stop working with the other cogs in the cell.

Harmit: And yet what we observe in reality is that many of these proteins, they're often as rapidly evolving as, you know, immunity proteins, which are rapidly evolving to keep pace with changing pathogens.

Harmit: So understanding why what we would refer to as housekeeping proteins evolve rapidly is really one of the underlying themes in my lab.

Harmit: And here's a cytoskeletal protein that a postdoc in the lab started working on because unlike other cytoskeletal proteins, this one tended to be very, very rapidly evolving.

Harmit: And we wanted to understand what the basis for that was.

Harmit: And as we characterized the protein, it became very, very clear that this was actually very abundantly expressed in the male germ line.

Harmit: And so we had really begun to believe that we were going to establish a function, a new function, if you will, for the cytoskeletal protein that was going to be important for some aspect of male fertility.

Harmit: But we knocked this gene out, and lo and behold, the males were more fertile rather than less fertile.

Harmit: So of course, when you see something like that, the first instinct is, okay, I'm going to repeat this experiment.

Harmit: It's not a trivial experiment.

Harmit: We did it again, and we did this at higher temperature thinking that that additional stressor would maybe reveal a defect.

Harmit: And once again, we saw that the males were between 30 to 40% more fertile than the wild type relatives.

Harmit: And so here we are with an observation, which is the complete opposite of what we'd expect.

Harmit: We have a gene that's actually rapidly evolving, but yet very highly conserved in Drosophila species.

Harmit: It appears to be really only expressed in the male germ line, at least to the levels of detection, yet the knockout of the gene is essentially beneficial for male fertility.

Harmit: Now, we were basically, of course, really worried that we had missed something very important.

Harmit: And so when we went back and we realized that there's actually very faint expression of this gene in early embryogenesis.

Harmit: And so we set a series of experiments where we basically checked the fertility of females that were knocked out for this gene, even though we could barely detect expression.

Harmit: And then we saw a really profound result.

Harmit: We basically got very few progeny and ended up discovering a pretty significant role for this gene in early development, which was completely contrary to what I would have told you for about 70% of the project.

Harmit: It ended up basically taking a complete detour from our expected path.

Harmit: And I give a lot of credit to the postdoc who recognized that one of our base assumptions was wrong.

Harmit: In this case, the assumption being that where a gene is primarily expressed is where it's most functionally important.

Harmit: And it is one of those things that sort of reminds you that we do make these assumptions all the time.

Harmit: In fact, we don't always even test these assumptions because they're so ingrained in what we learn.

Harmit: In this case, we were pretty lucky that we were able to close the loop because it was somewhat of a close ended project in the sense that it had to be something and it was just a matter of figuring out what that something was.

Harmit: Sometimes it's not so close ended.

Itai: Yeah, it's really interesting that you say that because I think in any project almost, you reach the stage of a contradiction.

Itai: You have this expectation that one more killer experiment and the paper is done.

Itai: And when you're confronted with the contradiction, you have to decide, what do you do?

Itai: Do you brush it under the rug or actually have the courage to go into it?

Harmit: I think every project in which we could claim to have made a significant contribution, there is an aspect of this.

Harmit: And that's partly because it's really only people who follow up on this observation and are really brave enough to challenge what the status quo is that can really lead the field in a new direction.

Harmit: But I also just wanted to point out that it takes the right circumstance as well to do that, where we both have the luxury of time and also there's the luxury of the willpower on the part of my postdoc Courtney Schroeder.

Harmit: Sometimes these projects are defined by just the archetypes of what leads to the project, funding sources, a certain timeline of how quickly this paper needs to be written, et cetera.

Harmit: And all of those things are often decided well in advance to the logical conclusion of the project.

Harmit: And actually that to me is perhaps the single biggest factor that I would argue maybe holds back pursuing these dark alleys.

Harmit: Sometimes the dark alleys are in fact dark alleys that we shouldn't really not have gone down, but sometimes the dark alleys are really the path to enlightenment and we don't really know ahead of time which one is gonna go unfortunately, but sometimes we are really forbidden to go down any of these dark alleys, partly because the mechanics of running a lab or actually like running a career in science sort of forbid you.

Harmit: So you settle if you will for the good enough kind of conclusion without really pursuing.

Harmit: That actually to me is like the big trade off to make sure that you are being a good scientist and following a project to its logical conclusion, but you're actually doing this without really sacrificing the best interests of the people who've chosen to work with you.

Martin: So you think that is more a limitation imposed by the need of the people actually working on the project who still have to progress in their career, or is that more something that's imposed by the funding agencies?

Harmit: I think it would be a mix of both.

Harmit: We definitely do have some type of science that is predictable in its trajectory.

Harmit: When a paper is going to be written in a sort of predictable fashion.

Harmit: And those types of projects are both extremely sought after and do well in terms of funding because of the predictability.

Harmit: But even those projects will give you some observation which you had absolutely not expected to find.

Harmit: And so the question is, do you write the paper with the deliverables that you had basically predictably expected to see, or do you wait to see what this unexpected observation will lead to before you write the paper?

Harmit: And often I think the challenge with the stipulations of funding agencies and training kind of advancement is you write the paper that you have and you hope that you'll go back and finish the logical conclusion and explain this weird observation that you were not really expecting to find.

Harmit: But the reality of the situation is that if you aren't careful, you suddenly accumulate a number of these weird observations, each of which could really be its own paradigm, but you have already moved on to the next set of big projects.

Itai: I think sometimes we blame the funding agencies, but I think we as a community of scientists should also take responsibility when we hear, for example, a grad student say, oh, none of my experiments are working.

Itai: I'm getting such contradictory results.

Itai: Well, if you hear that, you say, your response should be good.

Itai: That's great.

Itai: You stumbled upon something potentially really interesting.

Itai: So I think if we better highlight in our community that perplexity and contradictions are actually good for you, they're telling you that there is work to be done, that will be the source of other changes, like for example, the funding agencies also being more tolerant of open-ended projects.

Harmit: I completely agree with this.

Harmit: And I actually think that even just more honest storytelling in how we give seminars is a really good way for us to tell students who are watching us for the first time.

Harmit: I actually make it a point to really talk about my moments of anxiety.

Harmit: Practically every project that we do, we reach a point where we kind of failed, at least temporarily.

Harmit: We failed because we thought that we had a certain expectation and we did not reach that expectation.

Harmit: But just like Itai was pointing out, to us actually all of those have been the prequel to what I would consider a truly breakthrough finding.

Harmit: Where we recognize that our base assumptions, which are really shared by everybody in the field, are really wrong and we really forced ourselves to kind of look beyond that.

Harmit: And just advertising that aspect where we were really unsuccessful, at least in the beginning, but actually that was really hiding the ultimate success of the project of the ultimate creativity of the insight.

Harmit: I think we need to do that more.

Harmit: I think some of the best storytellers in terms of oral storytelling of scientific stories really do that.

Harmit: But actually, as you pointed out, that is completely squeezed out of the written narrative.

Harmit: And I'm not really picking on journals, but some journals don't do that.

Harmit: Current Biology, which is one of my favorite journals for exactly that reason, they're like weird findings.

Harmit: They don't actually have a logical ending.

Harmit: I've not actually told you at the end of the paper, here's the molecular basis of this kind of really cool finding, but I've told you the finding.

Harmit: And we need space for those papers because actually that's really where a lot of the creative phenomenology lies.

Harmit: And I think we've gotten so entrapped by the tools we have at our disposal to really dissect molecularly what's going on, that we've actually lost a little bit of that simple joy of discovery of weird phenomenon in biology especially.

Itai: That's true.

Itai: Now it's all, what's the mechanism?

Itai: What's the mechanism?

Harmit: In fact, it's like the traditional rejection letter that in the absence of mechanistic insight, we feel like your paper is not suitable for this journal.

Harmit: So that is another subtle kind of pressure to kind of do a certain type of science and not pursue a different kind of science.

Harmit: Even though ultimately it's that different kind of science that will end up being the one that really drives the paradigm.

Harmit: It's become cliche now to talk about this, but we think about CRISPR-Cas and many thousands of papers that have ensued from that, but it really started off with a very weird observation of these clustered repeats and their potential role as anti-phage defenses and bacteria.

Harmit: And there's a plethora of these kinds of defenses and even more are being recognized, but the insight to sort of view that and then recognize the value as a genome editing tool, I mean, that's true insight, right?

Harmit: But it's still built on these foundations of kind of clever but not fully mechanistically understood observations that were the prequel to that.

Harmit: And I think our cupboard will be very bare if we focus only on the mechanistic insights and not allow for these phenomenological insights to really be part of our literature.

Martin: So you said that initially you often fail in the project until you realized that really there's something totally different going on from what you expected.

Martin: But the insight that you failed, that's relatively easy, right, you don't get the results that you expected.

Martin: But then to figure out what is it that's really going on, that's where you really need to have some creativity.

Martin: And we're wondering, do you have a specific habit or any technique that you use when you try to understand something that you're not yet understanding?

Harmit: Really excellent question, Martin.

Harmit: I wish I could deliberately say what my technique is, but to be perfectly honest, my approach is to tell everybody about this paradox that we're facing.

Harmit: So anybody invited speakers come in and we have conversations, and some people love to tell them about the completely polished stories in which, we've totally worked out everything.

Harmit: We also, you know, I'm in a department which really values faculty kind of working on the bench, even though I do not.

Harmit: So we actually give each other lab meeting style presentations once a year, where we talk about work in the lab.

Harmit: And again, some people view that as an opportunity to give like their most recent polished seminar that they're basically giving other places.

Harmit: I view it as a place to really talk about something that I haven't figured out yet, because here's an opportunity for me to take advantage of all of my brilliant colleagues and share with them, okay, these are all the findings.

Harmit: So in a sense, I don't view it as a failure.

Harmit: I just view it as a work in progress, because to me, a failure is when an experiment failed technically.

Harmit: If an experiment gives you an answer, and you know that it's technically sound, it's a success.

Harmit: It's just not a success that you've actually fully put together in the jigsaw puzzle that it's intended to be.

Harmit: And often, actually, the insight doesn't come from other people.

Harmit: But just telling people repeatedly about what you're doing, some of these puzzles start falling into place.

Harmit: It's almost like the process of drawing on this chalkboard.

Harmit: I love this chalkboard.

Harmit: Actually, the thing that I miss most about working from home in COVID times is my big whiteboard, which is perhaps my single biggest luxurious investment in my office, that I repeatedly write what we have found, and what do we know, what's missing, et cetera.

Harmit: And just going through that process over and over with different people within the lab, outside the lab, et cetera, suddenly you recognize, or somebody asks a question, which makes you go, huh, actually, I don't really know that.

Harmit: Similarly, in the project that I told you about, somebody said, well, so what if it's maximally expressed in the male germline?

Harmit: Maybe that's not what the function is.

Harmit: And of course, that's something that we should really have been thinking about, but we were so enraptured by this three orders of magnitude higher degree of expression that we never even really considered that this low puny amount of expression, which was just barely above noise, could really be the functionally important thing.

Harmit: And it's just the kind of thing where even just telling yourself the same thing over and over, you begin to sort of question each step or each assumption that you made.

Harmit: And often that process where you sort of doodle, I actually take pictures of these chalkboard things where I, you know, after I've drawn something out, I'll take a picture and suddenly I have these cascading slides of multiple models that I've built.

Harmit: And certain models you realize you're making the same model over and over for the same part.

Harmit: And then you recognize that that's probably the place where you're making the false assumption.

Harmit: Because you know, the thing that you've not challenged is probably where the flaw lies.

Harmit: And I would say that 90% of the time that's turned out to be true.

Martin: So when you described that whiteboard in your office, is that like an evolving document about everything that's going on in the lab?

Martin: Or is it more something where you just sketch something while you're talking and then you wipe it off and sketch something different?

Harmit: Yeah, it's an excellent question.

Harmit: I actually use that whiteboard for two things.

Harmit: One is just a reminder of all the things that I really need to do, like letters of recommendation that are due or some tasks that are due.

Harmit: And that's kind of in one corner because it's something that when I'm in my office, I look at every day and it sort of reminds me that I really need to do that.

Harmit: But the other part is actually cleaned out every day.

Harmit: At the end of the day, I actually take a picture of what's on that whiteboard.

Harmit: So I actually have like a record that I can scan through on my phone when I'm sort of-

Itai: The evolution of the whiteboard.

Harmit: I'm looking at the evolution of the whiteboard, but I'm starting from scratch every time.

Harmit: So actually the whiteboard, when I'm thinking of a problem, ends up looking very, very similar.

Harmit: There are some sort of things that are quite different at the ends.

Harmit: What I was saying is that the parts that look really, really similar over and over really sort of tell me at the end that, look, I've not figured this out.

Harmit: So maybe it's in the parts that are really similar that I really need to challenge more.

Harmit: And often that actually turns out to be where the breakthrough is maybe lying is that, the thing that I've actually taken for granted is actually the thing that is perhaps wrong, rather than the thing that I'm constantly evolving.

Harmit: So ironically, the parts of the project that are intellectually most slow evolving are perhaps the part that really need more change.

Harmit: Whereas the parts that are rapidly evolving, they're flexible enough that they could actually accommodate a lot of changes.

Harmit: But it's also not just me writing on the right board by myself.

Harmit: I really find it useful to work in groups of two or three people.

Harmit: That's the ideal kind of really group for me.

Harmit: And often it's me and the trainee or me and a staff scientist in the lab where we're basically going through.

Harmit: And it's really great to be surrounded by people who really, I don't know if I can say this on the podcast, but they don't really give a shit about your assumptions or about you.

Harmit: It's really good to be surrounded by people who are not afraid to call you out.

Harmit: And because then it's not a differential, it's very much like a mutualistic kind of thing where they're saying, well, I don't really get this.

Harmit: Why are you making this assumption or why are you getting this?

Harmit: And it takes a while for people to get into that mode because they may have come from labs in which perhaps it was a little bit more hierarchical, and you were not really encouraged to really challenge the boss's assumptions.

Itai: Going back to the whiteboard, it brings to mind a conversation that Martin and I had with Ellen Rothenberg where she said that she was at her most creative and she could, quote, inhabit the data.

Itai: And I'm wondering if your visualization process with the whiteboard is kind of like your conversation with the data.

Harmit: In a way it does.

Harmit: I always write down the results of the crosses or what we found or what the rate of evolution in a particular kind of pathway is.

Harmit: And I write it down anew every time because it forces me to remind myself about what it is that we know is true and what it is that we basically don't know, but we are sort of framing into this thing.

Harmit: And it's actually really good to remind yourself about that.

Harmit: But as you write it over and over, then you realize, actually, I don't really know this.

Harmit: This is still one step away from what we observed.

Harmit: And that process I find really useful because it allows you to kind of go back and challenge some of the core assumptions behind your projects.

Harmit: So writing the results over and over, even though it seems like a failed exercise, it's a tedious thing, but I actually find it really useful to do that over and over and with different people because they each have a slightly different way of asking you about questions that you might be doing.

Harmit: And you know, I do this with my own projects, but actually what has really convinced me that this is a really good way to do it is that I've also done it with other people when they've come to me stuck in their problems, right?

Harmit: I just actually had a really awesome conversation on Monday with a colleague who's working on a bacterial recombination protein that I don't really even work on.

Harmit: So even asking him very base questions about like, how do you know this?

Harmit: How do you know this?

Harmit: And some of it is like, okay, you just need to know this, but it's actually really still good to tell people about what it is that we know based on what others have found.

Harmit: And I find that exercise to be really, really fun.

Harmit: The hard thing is to actually convince somebody who's not been through this with me that there is probably a good outcome at the end of this.

Harmit: You know, I've been through this a couple of times, and I think both of you have probably also.

Harmit: So you know that some of it is a little bit of intellectual arrogance, to be honest, that we're going to solve this.

Harmit: But actually, this is the most fun part of doing science, is solving these puzzles to me.

Harmit: This is why I got into science in the first place.

Harmit: So I don't lose sight of the fact that this is exactly what I want to be doing in the lab.

Harmit: You know, it's not just writing the papers and, you know, receiving accolades, etc.

Harmit: It's really the, you know, the nitty-gritty of this.

Harmit: And so I really enjoy it.

Harmit: I enjoy it even when I've not figured it out.

Harmit: I enjoy the fact that I've had a really good day, you know, and then I raise my blackboard after taking a picture and I go home.

Martin: Yeah, yeah.

Martin: So do you think that the added benefit of thinking together with other people is this challenging of each other's assumptions?

Martin: Is that the main reason why thinking together makes us sometimes more creative?

Harmit: I think also just telling people about your assumptions reminds you yourself about your own assumptions.

Harmit: And I think in a way, for me, actually the most useful thing is every time I tell people about the assumptions, I begin to realize, you know, on the fourth attempt or fifth attempt, actually, do I really know that?

Harmit: I don't really know that.

Harmit: I suspect that that's true, but I don't really know that.

Harmit: And I make a mental note.

Harmit: And then the next time when I'm telling the story, I have already got a question mark to that particular assumption.

Harmit: You know, so it's sort of, it's like the sacred cows in your assumption book.

Harmit: You begin to sort of take them a little bit down from the mantle piece by piece.

Harmit: And I find that very interesting.

Harmit: Again, you know, it's not always the case that others will solve the problem for me.

Harmit: But the act of explaining this to others really does help me solve the problem.

Martin: Yeah.

Martin: So, so far, you talked mostly about the facts.

Martin: You write down the rate of evolution for a gene, for example.

Martin: But is there also an aesthetic element to an idea that drives any one of your projects?

Martin: I mean, does a kind of elegance play a role?

Harmit: I would like to think so.

Harmit: But again, you know, I think we all have slightly different tastes in science.

Harmit: And one of the things that I really like to focus on when I'm interviewing, especially postdocs for the lab, because, you know, people who apply to the lab, everybody we interview is very, very qualified.

Harmit: But what I'm trying to really figure out is, do we have the same tastes in science?

Harmit: Because it's kind of really hard to find a way to overcome a mismatch in those states.

Harmit: Like I can find a way to overcome mismatches in training or overcome mismatches in the actual experimental skill set.

Harmit: But if I find something really interesting, and you're just not interested in it, it's actually going to be really hard for us to sustain this conversation.

Harmit: So I do think that it's a little bit of a curiosity to share some papers that have really inspired me and then I see what people think.

Harmit: And some people don't really get it, because they're like, well, what is the molecular basis of that?

Harmit: I was like, well, that doesn't matter, but look at this.

Harmit: And some people are pretty comfortable without putting balls and arrows in their flowchart, and some people are pretty uncomfortable without those in place.

Harmit: And it's not to say that both of those cannot contribute really well to a lab, but repeated mismatches in terms of this kind of taste mismatch could be really difficult to overcome.

Itai: In our sort of world, we found it really useful to distinguish between this Night Science that's a creative mode where I can now picture you at your whiteboard and you're listing your assumptions, looking for false ones and really trying to think deeply about the problem.

Itai: And we distinguish that from the Day Science mode, which is more the executive aspect of, okay, we've got this hypothesis, let's just figure out what strains do we need, what's the right cross, what's the killer experiment, the controls, the power, the statistics.

Harmit: I think especially if you're running a relatively big size lab, I think it's absolutely true that you really do have this Day versus Night Science mode.

Harmit: We sort of are kind of perpetually in the Night Science mode in our lab.

Harmit: We're kind of constantly in the nitty-gritty.

Harmit: And I don't say this with a sense of pride.

Harmit: It's just the function of the size of the lab.

Harmit: We have  benches, so we are capped at a maximum size of  independent researchers, which means that we really do have the time to focus on different projects.

Itai: You said that we're focused on the nitty-gritty as an aspect of Night Science.

Itai: Some people would maybe confuse that with the nitty-gritty being the Day Science.

Harmit: The Day Science in a way I view as the science that pays the bills.

Harmit: If you will, you know, like writing the grants, writing the papers, giving the seminars, doing administrative work.

Harmit: I sort of feel like I'm doing that to be able to do the fun stuff.

Harmit: I'm sure both of you recognize this that as you grow into a bigger lab and a bigger operation, you often find that your ability to actually spend time on actual nitty-gritty, the stuff that you really love doing, gets more and more precious because your day gets taken up by a lot of the other things.

Harmit: And I've begun to recognize how important it is for me to really carve out that sheer joy of being able to draw on the board by myself, et cetera.

Harmit: The other aspect of it is that sometimes it's really hard to let go of a problem, even though it's actually better for me to let go of it and come back to it, because actually that fresh perspective is really, really valuable.

Harmit: I mean, you hear about the metaphorical shower moment, right?

Harmit: Where you're taking a shower and suddenly something you've been working on.

Harmit: But it really is true.

Harmit: When you take a break away from it, suddenly some things kind of click in and it's really good.

Harmit: My big advice is always have a notepad handy.

Harmit: I do actually have a notepad, believe it or not, like right by my bedside, because sometimes I do wake up and write stuff down.

Harmit: I often don't know what I wrote in the morning because it's like total gibberish, but occasionally it's actually something very simple that allows me to figure something out.

Harmit: You know, I heard from other people Brenda Schulman famously leaves phone messages for herself in the middle of the night where she can actually come back to her office and receive an answering machine message that she left for herself.

Harmit: Now, of course, we would just leave a note on your iPhone or something that you can actually play back.

Martin: It feels much more elegant, I think, to call your office during the night and leave a message for you that you'll discover the next morning.

Harmit: Absolutely.

Harmit: I have never done that.

Harmit: But if you know Brenda, that totally fits her personality.

Martin: How do you distinguish great ideas that you would like to work on, that you have or that someone in the lab has, from those that you consider less promising?

Martin: Can you describe how you decide that an idea is worth pursuing?

Harmit: Actually, for me, I think about what the sort of intellectual space to grow around an idea is.

Harmit: So if it's a technical advance, is this really going to help labs other than mine?

Harmit: Then yes, we would do it.

Harmit: If it's an intellectual advance that would basically allow this particular postdoc to actually set up his or her own lab in a space that's relatively underpopulated, we would also do it.

Harmit: But we do actually explore a number of projects, perhaps more than we can possibly finish, with the expectation of a little bit of a milestone.

Harmit: Like, what do we need to see to convince ourselves that this is a worthwhile thing?

Harmit: Steve Henikoff, who was my postdoctoral advisor, always used to say, I love projects that fail quickly.

Harmit: I don't think he meant that in the literal sense, but what he meant was that, you know, it's really great to actually try a new idea, but you also really don't want to be spending four years before you discover that this idea was a dud.

Harmit: You really want to be in a place where you can identify a key experiment or a key finding that convinces you that you're actually on the right track.

Harmit: And I thought that that was a really important insight that I took away from his lab, the process of vetting what is a really good idea.

Itai: So, Harmit, I wanted to ask you one final question.

Itai: Is there an aspect of the scientific process that you would say is misunderstood?

Harmit: I think we've touched upon two of them already, which is that the science that we see presented in papers is often not the way the science was done.

Harmit: But I think the one aspect that people also don't understand is that there can be a cost to doing science that's really creative in the sense that we need to build in some probability of failure and actually support that, because otherwise we are basically going to get entirely predictable science, which is actually not really going to benefit anybody.

Harmit: And I think even the NIH and other funding agencies are recognizing the value of not really funding very closely defined projects in which all of the predictable outcomes are outlined as a five-year plan.

Harmit: Again, to quote Steve Henikoff, if I can tell you what I'm going to do for the next five years, and that turns out to be true, that's probably the most boring science, right?

Harmit: Right.

Martin: But isn't that what the funding agencies mostly expect?

Harmit: I think some funding agencies do expect that, because again, they're really high on the feasibility criteria.

Harmit: But it's also true that if you actually even just were successful in everything you propose to do, you probably would not do so well at the renewal stage because it was entirely predictable.

Harmit: So there needs to be a little bit of a marriage between feasibility and innovation that does come with some probability of failure.

Harmit: But even creative failures actually teach us a lot, but we don't really hear about that.

Harmit: So in a way, I'm sort of encouraged by people putting preprints of great ideas they had that didn't really work out as an example of something that they actually tried because we can actually all learn from that.

Harmit: But in the traditional mechanism of publishing, we really don't have an ability to do that.

Martin: So like a second role for biorxiv, for example, as a graveyard for failed projects?

Harmit: Well, again, I wouldn't say that they're failed projects.

Harmit: Remember, for me, a failed project is something that technically failed.

Harmit: It could be a graveyard for a project because you had a great idea, but it turned out you did the experiment really well and it didn't turn out to be what you were expecting.

Harmit: It's really good to actually have a repository of these ideas because others can build upon those.

Harmit: And we've actually had a preprint that we put out which was missing an element and somebody reached out to us saying that they'd love to collaborate with us on that element.

Harmit: And we ended up writing a really great paper because it was really a combination of an idea and some data we had and then the experiments that they could actually do to help us directly test our hypothesis.

Harmit: That's what made the paper really fantastic.

Harmit: And in a way, I would say that it's maybe not a graveyard so much, but the beginning of a conversation that will allow you to make for a really good collaboration.

Martin: That's actually a great perspective on these repositories.

Itai: Well, Harmit, thank you so much for joining us.

Martin: Yeah, this was a really interesting discussion.

Harmit: It was my pleasure.

Harmit: Thank you very much.