If I could start over as a PhD student today, in 2026, what would I do?
A conversation with a PhD student on deciding career trajectories, how to actually do science, science communication, and why bioRxiv is where the real record lives.
By Sophien Kamoun & Oscar Garrett
Recently, Oscar Garrett, a PhD student in Pam Ronald’s lab at UC Davis, reached out for a chat about navigating a scientific career in 2026. Toward the end of our call, we decided to document the discussion for a broader audience of early-career researchers. Below is our conversation, lightly edited from the transcript for clarity and readability.
Oscar Garrett: The essence of what I want to talk about today is essentially: if you were a PhD student today in 2026, knowing what you know now as a professor with a successful career, what would you do? In particular, starting with: would you go the academic route? Would you aim directly for an independent research institute like The Sainsbury Laboratory? Or would you go into industry, starting in a corporate structure or taking your chances in a startup?
Sophien Kamoun: Very good question. Thank you, Oscar, for asking me that.
I think it’s first a hard question to answer because, personally, I haven’t been very careerist in my trajectory. I didn’t really make decisions based on thinking, “This is the best decision for my long-term career path.” I went more with my intuition and the mood of the moment.
For instance, I ended up doing my PhD at UC Davis, in fact about the same time Pam Ronald, your PhD supervisor, did her PhD with Brian Staskawicz at UC Berkeley. And that was more because I grew up in Tunisia, I was studying in Paris, and I really dreamt of living in California, right? It was much more driven by that than, “Oh, Davis is a great place to do plant pathology.”
I also got into plant biology a little bit by accident because I received a fellowship for my PhD, and that fellowship required that the PhD be on plant biology. That was really the reason. It wasn’t like I calculated that plant biology would be super cool.
In the same way, I became a biologist because I grew up as a natural history buff. I was collecting insects and catching butterflies and stuff like that as a teenager, and I really wanted to be a biologist. Little did I know back in the ’80s that biology would be undergoing this massive boom, an explosion, and become the science it is today.
I think intuitively in the back of my mind (and this is maybe the part that’s kind of interesting, looking back at it now), I knew DNA had been discovered and molecular biology was growing and becoming a really impressive science. As someone who was curious and reading a lot of popular science, I probably knew intuitively that biology would be big. But I don’t think I consciously made the decision to become a biologist because I knew that 30 or 40 years down the road it would be this massive science it is today. And now you know how valuable it is to be a biologist today, right?
“Trust your intuition to some degree. If you’re a curious mind and you’re reading and learning something new every day, which frankly these days with the availability of information we have no excuse not to do, then you should trust what’s going on in your subconscious mind in terms of analyzing all of this.”
Maybe that’s a long prelude to answering your question. Otherwise, today it’s complicated, isn’t it? We know what’s happening in academia in the US in particular. It’s really suffering. Universities are being destroyed by the current administration. They just hate academics, and they’re really destroying something beautiful. I grew up in the US academic system, and I know how valuable it is. When I was a kid, there was this appreciation that the only place in the world you could go and study butterflies if you wanted to was the US. They’d fund you to do that. It’s not totally true; there were other places, of course, but the US seemed to be the most accessible place to go to basically do curiosity-driven research, which is really the best type of research.
So I’m going to rephrase your question. The first question to ask yourself is: Do you want to do curiosity-driven research, or do you want to do more goal-oriented or problem-oriented research?
Oscar: Yeah, in my case, I’m a little bit of a fence-sitter. I’m definitely driven by problems, but at the same time, I’m interested in what those problems point to at a basic biology level, or solving problems in order to get at basic biology, that kind of thing.
Sophien: Yeah, and I think that should be part of the equation, shouldn’t it? Because academia should be about curiosity-driven research. The best academic environments are the ones that allow you to pursue unexpected findings, no matter what direction they take you. You aren’t constrained by a company’s objectives or by what research will lead to a product.
Even some institutes can be very constrained. I hope not ours, but some institutes can be constrained culturally because, say, “We’re an agriculture institute, and so we have to stick to agricultural problems.”
A good example of corporate constraint is the discovery of CRISPR. That first happened in a company, Danisco. Their yoghurt cultures of Streptococcus thermophilus were dying from phage infections in the fermenters. They started studying that and discovered CRISPR. They patented it for phage resistance in starter cultures, which is what they needed, and left the rest of it on the table.
So you want to ask yourself what kind of environment you want to be in. That should be driving the equation. But I see your point. I think a lot of students at your stage of their career and life are kind of on the fence. Curiosity-driven research is also tough, right? Because you don’t know where you’ll end up. It could turn out to be boring, too. You might never come across anything really amazing. So there’s a lot of risk associated with that, and you have to think about what matches your personality.
The only difference I would point out compared to my generation is that you have a lot more options. When I got my PhD in the early ’90s, in 1991, startups weren’t really a thing in biology as they are today. Industry existed, yes, with established companies, but that felt like a one-way street. You’d be working in a very constrained technical environment. You’d definitely gain some managerial experience, but it felt like if you went that route, that was it. And research institutes back then were much more academic than they are today. Now, there are all kinds of institutes that ideally sit in the space between academia, startups, and industry.
So I think, especially if I were in the US right now, I would probably not consider a typical postdoc. Maybe I’m going to upset a lot of people by saying that, especially the ones who are recruiting! But I think there are a lot of alternatives now: more creative startups, all this AI stuff that’s popping up, which is very exciting, and hybrid models like commercial startups that are built like research institutes. Because there are so many more options, I’m not sure what would be the single best choice. Everyone is different, so there are different best choices depending on the person.
Oscar: I’ve always personally been really interested in independent research institutes. So a quick follow-up would be: how did you find yourself as a Group Leader at The Sainsbury Laboratory?
Sophien: How did I find myself here? Well, I went to Ohio State first. As you may know, I spent nine years there, and that’s where I started my lab. And I think that was a huge advantage, to be honest, because it wasn’t a high-pressure kind of environment.
If you’re in a more high-profile environment where your next door colleagues are getting big grants and publishing big papers, you may start trying to follow trends to keep up. At Ohio State, I felt like I could take risks. So I worked on Phytophthora. Literally, people were calling it a “geneticist’s nightmare.” There was a renowned scientist at the time who was basically telling their postdocs, “Never work on Phytophthora, you can’t make knockouts, it’s useless.”
So I felt like I could actually take risks and work on that. And I wasn’t the only one. Saskia Hogenhout, my partner, who is now at the John Innes Centre next door (also in an institute), started working on phytoplasmas, which are unculturable bacteria. For microbiologists and bacteriologists at the time, that also seemed crazy: “What, you can’t even culture them? Can you make mutants?”
If I had been in an environment where I had to chase the big grants and the big papers and all of that much more aggressively, I would have been more constrained. I might have started doing what sadly too many people did in the plant biology field at that time: making Arabidopsis mutants and misinterpreting them just to get the papers published. There are hundreds of papers like that where people published pleiotropic mutants of Arabidopsis and said, “Yeah, this is involved in immunity,” even though it’s just a pleiotropic mutant.
Instead, we did something creative and original. That is what allowed me and Saskia to create our own scientific identity and made us competitive for getting the positions here, because we had an identity. We weren’t yet another plant immunity lab knocking out yet another gene and describing the phenotype and blah, blah, blah.
And then, of course, effectors were discovered. I didn’t predict that. Who knew it, Phytophthora could have very well turned out to be a one-toxin-type pathogen and things would have been boring! But then there were these hundreds of effector genes, and they were very interesting.
There was also the realization that effector biology is plant biology. So it doesn’t matter whether your pathogen is tractable or not. You can express the effectors in plants and do some really cool stuff with that, which is exactly what we did. Some people came to effector biology more from the pathogen side. They thought that making knockouts would help them understand how effectors function. Not really. Even in bacteria like Pseudomonas syringae, where you can make knockouts, it’s generally hard to get phenotypes with single effectors.
And others came from the Arabidopsis side and actually really disrespected Benthi (Nicotiana benthamiana), my favorite system. I owe my career to Nicotiana benthamiana. For me, realizing early on that Benthi was an amazing system was crucial. And it’s amazing because it shortens the experimental cycle, right? You infiltrate on Friday, you have your result on Monday or Tuesday, and by the next Friday you start another experiment. You can kill a lot of hypotheses that way.
I think a lot of people don’t appreciate that. Let’s say, you’re doing cell biology, for example. Try to do cell biology in Arabidopsis: you have to make stable lines, and you have to wait several months for the transformants. And then if you want to co-express different constructs, it becomes impossible to manage. But with Benthi, it’s super quick and powerful. Tolga Bozkurt, who’s now at Imperial College, calls it fast-forward plant cell biology, and he and Sebastian Schornack figured out how to image haustorial interface in transformed Benthi leaves.
“What worked out was just using common sense, really, and not following the crowd. Don’t follow the herd. That’s my advice: don’t follow the herd.”
Oscar: Oh, and I have a really quick, selfish question: have you seen data for knockouts of AVR-Pik from Magnaporthe, and was there any observable phenotype?
Sophien: I don’t think there is a virulence phenotype, actually. There’s too much redundancy, especially with those HMA-binding effectors. It looks like Magnaporthe has tons of those HMA targeting effectors.
Oscar: Yeah. I figured that was the case, but I haven’t seen it published.
Sophien: Yeah. I think you have to go back to the good old Brian Staskawicz kind of insight: you’re going to clone AVR genes not by mutating the virulent or even mutating the avirulent race, but by moving the effector by complementation from an avirulent to a virulent strain, or race, of the microbe.
It’s funny because a lot of people who come to this from microbial genetics are obsessed with knockouts, and they don’t respect complementation enough, even though it is literally the same thing as a knockout! Basically, you have isogenic lines or strains of the microbe, and you compare them. So it doesn’t really matter much whether it’s a knockout or it’s a complementation; it’s still isogenic.
If you want to push this paradigm even further, I would argue that heterologous expression is a form of complementation, too. If you express an effector in a plant and you have a phenotype, that’s a form of complementation. Of course, you need more data to conclude.
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But I do feel like one of the problems in plant biology (and I’m old enough to know this) is that there were maybe two decades where geneticists dominated aggressively, and really misused genetics. Massively misused genetics.
Do you know the story with the rabbit metaphor of doing genetics on a rabbit? You shine a light on the rabbit, and the rabbit hops, right? Your readout is basically the light response: the rabbit is hopping after you shine the light at it. Then what you do is you break the leg of the rabbit, you shine the light, and the rabbit doesn’t hop. And you write a paper saying: “Legs are important for light response.” The second experiment is you take the rabbit, you ablate one of its eyes, and then you shine the light. The rabbit hops. And you say: “The eye is not important for light response.”
In plant immunity, there are literally hundreds of papers like that. And I think they’re useless. Honestly, I’m happy to go on the record for that. They’re useless papers because you need more data. You need biochemistry, you need cell biology, you need evolutionary biology, and you need more comparative analysis to interpret this phenotype. If a mutant has a pleiotropic phenotype, you have to be honest about it: describe the full range of defects and consider indirect effects. Take a mutant that doesn’t form root hairs. You inoculate it and say, “Oh, I’m getting far fewer nodules.” What does that tell you? Does that make the mutated gene a “nodulation gene”? Or could reduced nodulation simply be a consequence of the root-hair defect?
Oscar: Very good points. Okay, so the next question I have for you: suppose you’re still a PhD student in 2026, and you have a good amount of time for new technical training. What kinds of technologies are most exciting to you for their promise to make a difference, particularly in solving crop disease?
Sophien: I mean, it’s not complicated these days. It’s anything AI, right? We’re right in the middle of this AI revolution. It’s changing almost every week, and there are new tools popping up constantly.
If you’re a biologist, biology is an information science. Everything is coded in the genome. I’m a firm believer in that. Any tool that allows you to extract more out of genome sequences and genome data in your work is an example of that. Anything that allows you to do that, you have to invest in. And I think AI is really amazing at turning genomics data into something useful. I really believe that it will be very easy with AI to discover new patterns in genomes: new information that is coded in the genome, but that we haven’t been able to access yet.
If you think about it, AlphaFold is an example of that. You start with a sequence, and you don’t just end up with the protein sequence; you end up with a structural model. You’re getting even more out of your genome sequence data.
And now the next frontier is PPIs, or protein-protein interactions. You start with two genomes, or even one genome, and you identify all the interactions. I do think anything that allows you to basically get more information out of the genome code is worth investing in, learning, and expanding your skills into. And I feel that’s a problem that is already being massively impacted by AI.
Oscar: Yeah, I agree.
Oscar: And then the next domain that I’m interested in would be science communication. Regarding science communication, how much time do you think a PhD student should spend communicating their science, and what mediums do you think would be most effective today?
Sophien: It’s a good question, because I think that’s a tough balance. As a PhD student, you should first not lose the plot and focus on what you’re supposed to do first, which is research: learning to be a really good scientist, a really good researcher, and producing outputs that allow you to demonstrate that you indeed became a good scientist and know how to do science. I think that should be the number one priority. If that comes at the cost of other activities, I think that’s fine; you can always do them later.
Sometimes I do see some PhD students get too distracted by other activities. If they can manage to do it all, that’s fine, that’s amazing, that’s wonderful. I’ve seen students do that and be absolutely amazing at both the research and the other activities. But I don’t think it should come at the cost of your own research and development as a scientist.
This said, I always argue that part of our job is to communicate what we find and discover, and that should definitely be part of our learning. So you have to learn at least to write papers, right? Sometimes people forget it, but writing research publications is also a form of science communication. You don’t want to neglect that and move straight to popular science communication. We should not forget that giving good talks and writing good research papers are also forms of science communication, and that’s something you really have to build first.
I don’t know how much time you should spend beyond that; it really depends on how good people are at multitasking and all of that. But I think what is maybe more important is to try to learn as much as possible about the business of doing science. I don’t mean business as in commercial stuff, but: how do you get grants? How do you network? How do you build your career?
Actually, what you’re doing right now in talking to me is a very good sign. You’re paying attention to things that go beyond what a regular PhD student would do. Why not reach out to someone and have a chat with them? It’s not going to hurt you, right? Some people complain, “Oh, my lab doesn’t have money to send me to a conference.” Well, you’re having a much better discussion with me right now than if we met at the MPMI Congress! So why not reach out to people, network, and use social media?
“Here’s one thing I think is important for early-career scientists, whether PhD students or postdocs: Don’t be invisible.”
Maybe you don’t want to be tweeting like I do, ten times a day, but don’t be invisible either. Be present. Create a network. Make sure that people are actually aware of who you are. Communicating your science that way is probably worth some time.
One of my mentors, my cousin Malek Kamoun, an immunologist at Penn, told me this very early on when I was a PhD student: “The most important thing is that your name is everywhere.” And I was like, “What?” He said, “Yeah, just so that if people see your grant or your paper, they actually know who you are, and you’re not an invisible name.” And I think that’s not a bad tip.
Oscar: Yeah, that’s a pretty good tip.
One last question for you: is there any other advice that you wish you had heard earlier on in your PhD career that would have spared you some harsh lessons or pain?
Sophien: Yeah. I think the most impactful blogs I wrote were the ones about how to do science and how to be a scientist. And I think there’s not enough of that being taught at the undergrad level and the PhD level. We get very quickly focused on the technical aspects, rather than how to do science, and actually having honest discussions about the challenges that come with doing good science: the fact that experiments fail all the time, that you may not validate your hypothesis, and how to deal with that.
One of the most common questions I get when I do workshops is how to deal with negative data. And then I ask back, “What is negative data?” And people are often confused. Sometimes they say, “Oh, it’s getting a result different from the one I was expecting or hoping for.” And I’m like, “That’s not necessarily negative!”
I never had that training. Even though I studied at top institutions like Paris Sorbonne and then UC Davis for my PhD, nobody ever told me about how to deal with failed experiments, for example.
And I think it’s especially hard now, with the pressure that I didn’t have as a PhD student. Today, when you publish a paper, it’s massive: you are expected to have those six or seven figures with so many panels in each of them, and then you have 20 pages of supplementary material. I mean, this is insane! It’s almost beyond what a PhD student should be producing. Everybody is focused on just generating data, data, data without even caring about the quality of individual experiments. The necessity for orthogonal replication and all of those things are just kind of thrown away, and then it’s just piling up all kinds of data, sometimes of suspicious quality.
We’re not having enough of an honest discussion about this, mainly because the PIs are also under pressure to generate a lot of data, and they’re passing on that pressure to their trainees, their PhD students and postdocs. And maybe now we also have a generation of PIs who came through that system, who basically were treated like that when they were PhD students, and now that they’re PIs, they’re just doing more of it.
I don’t know if you came across the last workshop I did a couple of weeks ago at the University of Cologne. I wrote a blog about it titled “How Do We Recognize World-Class Science?” We ended up having a two-hour discussion with early-career scientists, and it was really good. I don’t think they’re much exposed to these kinds of discussions. It’s something I ended up building on my own through reading, discussions and my own experience, because nobody ever came and offered me a workshop saying, “Hey dude, you’re a first-year PhD student, this is how you should be doing research.”
It’s almost a taboo topic because, indeed, a number of molecular biology labs just expect their students to pile up data no matter what the quality is. I call it “Deliveroo science,” where the student is expected to deliver a preconceived set of data to the PI rather than truly discovering the truth, the reality of the natural world. I think we’re not having a proper discussion around the topic.
Have you ever had something like that? Actually, I’m curious: have you ever had a workshop about how to do science?
Oscar: Not something very intentionally, no. It’s just sort of figuring it out as you go. We certainly haven’t had any workshops necessarily covering these topics, so it’s definitely good that you’re giving those, and I hope there are more of them in the future and that other people catch on so it can spread wider.
It’s something that I’m experiencing firsthand, too. People don’t necessarily want to publish an absence of a phenotype, for example, as I was talking about with the AVR-Pik issue. I’m curious, though, if you’ve come across any outlets for that kind of thing, for saying, “Hey, I tried this and nothing interesting happened.” Would you consider bioRxiv to be a viable outlet for this kind of thing?
Sophien: Yeah, I think bioRxiv definitely is a go-to place now for that type of work. We have a number of papers on bioRxiv that will never be published in journals.
For example, it’s very difficult to publish contradictory results. We have two or three of those on bioRxiv, maybe more, going back over ten years now. When you try to publish those in journals and you’re contradicting an already-published study, it’s Brandolini’s law, known jokingly as the Fourth Law of Thermodynamics: the amount of energy it takes to refute a paper is an order of magnitude more than it took to produce it.
You get buried. They usually send it to the authors of the original study, and then you get ten pages of reviews. Literally, we got that over something that was totally wrong. And then I remember my postdoc saying, “I’m not going to spend a year doing experiments just to prove to these guys that they’re wrong, when I already know they’re wrong anyway.”
So for things like that, we just left them on bioRxiv. They’re there, and they did their job. A lot of people in the lab said, “Hey, you know what? It did the job.” For anyone in the community who wants to know, it’s out there.
I think too many people are chasing the journals these days. It’s easy for me to say at my stage of my career, of course, but I also have people in my lab who believe in that and they’re doing fine. They’re getting grants and fellowships and jobs and all of that. I think building your own reputation around quality is what matters in the longer term.
In fact, bioRxiv is the best source to find out how people really operate. If I want to evaluate someone, I’m going to go to the bioRxiv version, which is your own personal version, rather than the one messed up by reviewers and editors.
And I think there’s also a lot of suspicious science being published that is bypassing bioRxiv intentionally. In my blog, How Do We Recognize World-Class Science?, I have examples of experiments in top-tier journals that are absolutely terrible, and these papers haven’t been preprinted. Otherwise, it would be easy for anyone to say, “Hey dude, you’re missing controls here.” Instead, they bypass preprinting and end up in Science, Nature, or Cell.
So yeah, I think bioRxiv is an important outlet for any type of work, and I would encourage you to use it. I mean, impact is really how people are influenced once they read the paper, not about where it’s published.
Oscar: True, true. All right, well, this has been very enlightening. Thanks a lot again for joining me for this chat.
Sophien: Thank you, Oscar. It was fun talking to you!
For the record: Oscar sent a cold email to a professor he’d never met. That’s the entire origin story of this post.
My inbox still works.
This post was written with assistance from Claude and ChatGPT. It is available on a CC-BY license via Zenodo.
Cite as: Kamoun, S., & Garrett, O. (2026). If I could start over as a PhD student today, in 2026, what would I do?. Zenodo. https://doi.org/10.5281/zenodo.23888599
