Test tubes with bubble wrap and cardboard box on dark wooden table.

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Some research projects arrive gracefully at a natural conclusion, such as when a trainee leaves the laboratory. Others come to a screeching halt when funding runs out. Still more dance along the edge of viability, daring lab heads to pull the plug and move on. Four researchers share best practices on deciding when projects should end, and how best to wrap them up or redesign them. They advocate using approaches that ensure that colleagues’ interests, feelings and career prospects are protected in the process.

MARÍA CLARA INGARAMO: Make use of your professional circle

Postdoc, National University of Litoral, Santa Fe, Argentina.

A project can end for various reasons, including getting scooped by competitors or when funding runs out. In Argentina, we often face limited research funding compared with other regions of the world. A typical grant provides only about three million pesos (roughly US$18,800) for three years. This is often not enough to buy chemicals and pay for research staff and students. Furthermore, because Argentina does not manufacture many of the chemicals and equipment used in science, import fees can add up quickly. The weakening of the peso against the US dollar is also a problem. I know a couple of researchers from Argentina who ended their projects and headed overseas for better career opportunities.

I think ending a project can have different meanings to different people. To me, I like to think of ended projects as being deprioritized — I can always return to the idea at a later time. As a PhD student at National University of Litoral from 2016–21, I was studying the role of the p53 gene and protein in the metabolic regulation of adipose fat tissues in Drosophila. However, when I collected the metabolomics data, I was overwhelmed by the plethora of regulatory pathways of enzymes. I simply did not have the right expertise to manage and interpret the huge data set.

I ended up deprioritizing the project for eight months. During this period, I consulted my fellow lab members to get support with experiments and data analysis. At the institute’s weekly seminars, I asked for suggestions from colleagues studying metabolic enzymes. Eventually, I sought out a collaborator — geneticist Norbert Perrimon at Harvard Medical School in Boston, Massachusetts — who was able to provide me with guidance. I even joined his lab group for a year to conduct more follow-up experiments. I think that, before permanently ending a project, it is useful to consult your professional circle, either to reassure you about your decision or to find alternatives. It is OK to pause projects and resume them after you acquire new knowledge, techniques and training.

In 2021, I took three months of maternity leave the last year of my PhD. I had to end my part in the project and hand it over to a colleague. To do so effectively, I shared with him my experimental protocols, organized shared folders for data and had continual e-mail, text and audio exchanges. When my maternity leave ended, I took over the same project from where he ‘ended’. Maintaining consistent communication with lab members enabled me to stay updated with the project progress and resume ownership of it when I was ready.

XIAODONG CHEN: Redefine a project instead of ending it

Professor of materials science and engineering, Nanyang Technological University, Singapore.

Ending a project is not easy, because there are often multiple students and collaborators involved, each of them with different stakes in the work. If a project gets dropped, it could affect a graduate student who has spent the past three or four years working on it more profoundly than it would a senior faculty member who has multiple other projects running.

Instead of telling a student that their project has to end, I personally think it can be helpful for supervisors to explain it as ‘redefining’ their work. In my lab, most of our ideas might not work out, but ego or pride could deter researchers from willingly ending their projects entirely. By packaging how I assessed their projects in a more positive way, such as telling them that it is OK to publish negative outcomes, I can convince them to rethink and redefine their work to reflect what the data are suggesting, rather than clinging to their original idea. I also advise my students to talk to experts in my university and research field, and to carefully and critically examine how the project can be redefined and still remain impactful.

But when a project cannot be redefined, or must come to an end for some other reason, then I make sure to have a deep discussion with the student to explain why this is the case. In 2014, my group discovered a way to fast-charge batteries, and we even created a start-up firm to commercialize the technology. However, our start-up failed, because we were not able to manufacture the materials at the scale that companies wanted. This experience made me realize that some cannot be redefined, because the technology is not ready to make an impact.

However, this did not prevent the project from being revived. In 2016, a PhD student joined my lab and was interested in the project and in 2020, we finally found a way to scale up the production of the materials so they could be assembled into fast-charging batteries. I was able to revive the project because my student and I believed in the idea and in each other.

Molly Shoichet in the lab with the hydrogel that she and her group invented.

Molly Shoichet changed the scope of her lab’s research to focus on biomedicine.Credit: Roberta Baker/University of Toronto

MOLLY SHOICHET: Learn to let go and help transfer knowledge

Professor of chemical engineering and applied chemistry, University of Toronto, Canada.

Over the 27 years of my career, I have witnessed the end of many projects, often for good reasons. For example, when I started my lab at the University of Toronto in 1995, I tried looking into modifying fluoropolymers, a class of polymer that I researched for my PhD, for biomedical applications. However, I soon realized that, whereas the modified fluoropolymers were more useful for industrial applications, their biological effects were difficult to predict or control. At the same time, the scope of my lab was evolving to focus more on health and biomedicine.

In 2009, I decided to end our fluoropolymer research completely, not because of a lack of funding, but because of my new academic interests in therapeutics delivery and drug testing. I would advise early-career researchers to explore different research areas, but be willing to end projects that are less promising or of less interest.

I’ve also ended projects after realizing that my approach is not practical. Glaucoma is a disease in which increased pressure in the eye results in optic-nerve damage and ultimately, blindness. I tried to engineer elastic peptides that could be injected around the optic nerve to strengthen it. Although the engineering idea was cool, I realized after talking to biologists and clinicians that the complexity of the biology meant that this approach probably would not work. I would advise students to consult various stakeholders for their opinions before starting and ending projects.

Projects also end in a lab for other reasons. In 2019, Mike Cooke (a former postdoctoral fellow in my lab) and I co-founded the company AmacaThera, based in Toronto, where I am currently the chief science officer.AmacaThera’s product is an injectable hydrogel for therapeutic delivery into the central nervous system. While my research group continues to advance the fundamental biomedical-engineering aspects, the start-up is scaling up manufacturing and demonstrating clinical safety. The research ‘ended’ in our lab only to be handed to a commercial partner to further develop the technology for translational impact.

Knowledge retention and transfer is key to any research lab, but can be difficult when a project’s lead researcher leaves. To enhance knowledge transfer, I typically try to pair an incoming first-year PhD student or postdoc with a senior lab member who will probably be leaving, such that the researchers overlap for about one year. Ideally, the pair would work closely so that, when a paper requires revision, the new lab member can take care of it. I also have technicians who provide institutional memory for previous protocols and strategies. Lab notebooks, physical or electronic, are useful resources to restart projects that ended when lab members leave and are busy with their new jobs.

DRAGANA SAVIC: Avoid emotional attachment to ideas

Co-founder, INIA Biosciences, Oxford, UK.

During both my PhD and postdoctoral work, I had to end several projects. Sometimes terminating projects would be devastating if I had invested time, effort, resources and even emotions into them. Sometimes I was accountable to other partners and collaborators, too, and communication needed to be clear. For example, I was studying the role of carnitine, a molecule that transports fatty acids to the cellular organelles known as mitochondria, in various tissues. I was juggling between imaging carnitine in vivo — which I could do in the lab — and sending samples of extracted carnitine for ex vivo investigation by collaborators in another city.

Often, there were logistical constraints, because the samples had to be delivered in a timely manner. I felt that I needed to stay in control (rather than waiting for data from collaborators who had other projects) and do what I could in my lab to achieve my PhD goal in time. In the end, I decided that I would exclude the ex vivo data from my PhD thesis before initiating collaboration, to reach a common understanding on the expected outcomes and timeline with the collaborators. Throughout this process, I learnt to be objective and more efficient in my PhD work, by terminating experiments that weren’t panning out and moving on to a different one.

Many academic researchers are emotionally invested in their projects, which is great — you want to love doing what you do, but there is a fine balance between being persistent and being stubborn. A friend who was studying a particular drug for a few years encountered such a problem. He tested it in a preclinical pilot study, which produced mostly negative results, but he nevertheless took it to a larger study. This didn’t show any particularly significant results, which led to a loss of resources and time.

It is also crucial for researchers to understand that their projects do not define them, and ending an underperforming project can be beneficial because it frees up resources for other activities.

In academia, poor-yielding projects can essentially continue if the principal investigators and researchers wish to retain them. However, in start-ups and industry, when the costs of product development are too high — when products do not generate more value to patients than existing, competing products for example, or when they fit too poorly to the market — the project will be terminated without question. Ending projects is a lot more straightforward.

In my own start-up, INIA Biosciences, my team and I originally planned to create a medical device that can both monitor and treat immune diseases. We wanted to monitor cytokine biomarkers in blood and provide a non-invasive therapy to suppress the immune system. However, after speaking to investors, vendors, patients and subject experts, we decided to focus on the therapeutic aspect and ended essentially 50% of the initial business idea on cytokine monitoring. Now INIA is in the fundraising phase. I think this strategy is useful because it allows us to present a focused business idea to funders and investors, and devote resources to the most promising idea to generate the best possible outcomes. If this ruthlessness can be practised in academia, it could greatly enhance research productivity and impact.