In many conversations across our community today, one concern surfaces over and over again: the sense that curiosity-driven basic science is being squeezed by a growing emphasis on translational and applied research, as indicated by shifting funding priorities and institutional mandates. The language of impact, deliverables, and commercialization timelines is becoming more prominent. For many basic scientists, this feels like a loss – an erosion of the intellectual freedom that has long energized fundamental biological research.

I understand this concern and it’s real. I have spent my entire career as a basic scientist, motivated primarily by curiosity on how cells work. I am deeply convinced that fundamental discoveries can broadly impact downstream biological and biomedical applications, and I have refrained from “pigeonholing” my research into specific applications and potentially reducing the impact of the results. However, as I get older and as science advances, I increasingly appreciate the intersection of basic and translational research as a powerful opportunity for discovery, innovation, and intellectual satisfaction.

At first glance, basic and translational research are often framed as opposites. Basic science is described as open-ended and unconstrained by immediate utility. Translational research, by contrast, is often portrayed as goal-oriented, application-focused, and shaped by external needs, whether clinical, commercial, or societal. Although this framing is convenient, in practice, the boundary between the two is far more obscure than the simplest assumption.

Even research we proudly label as “curiosity-driven” rarely arises in a vacuum. Beneath our stated questions, there are often deeper motivations shaped by personal experience, societal needs, or historical context. When I was a graduate student, I worked on understanding whether cells possess checkpoints that can halt mitosis when something goes wrong. At the time, my daily motivation was driven by curiosity: what signals enforce order during mitosis and how do they control regulatory network of the cell cycle? But underlying that curiosity was a broader concern—how errors in cell division lead to aneuploidy, and how aneuploidy is associated with cancer. The research was basic in every operational sense, yet it was not disconnected from disease or application.

This is often how basic science works. We ask fundamental questions not because we expect an immediate application, but because we sense, sometimes intuitively, that understanding these mechanisms matters. The path from discovery to application may be long and unpredictable, but the motivation is rarely detached from the needs of the real world that we live in.

It is rightly celebrated that curiosity-driven research has yielded some of the most transformative advances in biotechnology and medicine. The discovery of CRISPR is a fantastic example: a fundamental investigation into bacterial defense mechanisms that ultimately revolutionized genome editing. Stories like this reinforce the idea that basic science, left unconstrained, will eventually deliver applications we could not have imaged.

What may be less appreciated, however, is the reverse pathway: cases in which a specific practical or application-motivated need actively drives new basic discovery. The development of induced pluripotent stem cells is a powerful example. The initial goal was practical – to generate pluripotent stem cells without relying on embryonic sources. Yet in pursuing that goal, researchers revealed something profound about cellular identity: that differentiated states are not fixed, and that a small number of key factors can reprogram cell fate. What began as an applied objective fundamentally reshaped our understanding of developmental biology and cellular plasticity. These examples remind us that translation does not just follow, but can also ignite, discovery.

In my own career, this has become increasingly clear as I have begun to engage more directly in translational projects. Of course, one motivation is the desire to generate tangible value and impact for the society that has supported my research and career. But two other motivations have been equally important.

The first is validation. As scientists, we observe, model, and interpret. We build conceptual frameworks to make sense of data. Yet there is always uncertainty about how complete, or even how correct, our understanding truly is. When a technology or therapeutic strategy derived from a scientific theory actually works in the real world, it provides a uniquely powerful form of validation. Few things test the robustness of our ideas as unforgivingly as reality does.

The second motivation is discovery itself. Translational efforts are remarkably good at uncovering what we do not yet understand. When we attempt to turn a biological insight into a working technology or intervention, hidden roadblocks are exposed and unanticipated variables emerge. In the process, new questions surface, sometimes deeper and more interesting than the ones we started with. More than once, translational efforts to move a discovery “forward” have sent us back to the drawing board, asking more or different fundamental questions.

Finally, there is also a practical reality that cannot be ignored: funding. The current constraints on basic research funding are real, and they affect investigators at all career stages. In this environment, diversification is not a luxury but a necessity. Industrial partnerships and translational funding streams represent an increasingly important resource. Importantly, many companies are now delegating substantial portions of their research and development to academia, creating opportunities for basic scientists to engage with applied questions without abandoning their intellectual identity.

My own laboratory has benefited from this shift. Industrial funding has supported work aimed at addressing specific, translationally relevant questions that a funder posts. At the same time, it has allowed us to pursue unexpected observations that arose during that work – observations that would likely have gone unexplored under more traditional funding mechanisms. In at least one case, this led us to an unanticipated and genuinely exciting basic discovery.

None of this is to suggest that all basic science should become translational, or that curiosity-driven inquiry needs to justify itself through application. That would be a mistake – fundamental

discovery remains the wellspring of progress and innovation in biology. But I do believe we should resist fearing translation as a threat to curiosity. When approached thoughtfully, translational engagement can sharpen our questions, test our understanding, and open new terrain for curiosity.

For trainees and early-career scientists in particular, it is worth emphasizing that embracing translational opportunities does not require abandoning depth, rigor, or curiosity. On the contrary, translational efforts are most effective when they are grounded in a deep mechanistic understanding, allowing problems to be addressed at their root rather than through superficial or empirical solutions.

As a community, ASCB has long championed the value of fundamental cell biology. We should continue to do so unapologetically, but at the same time, we can also encourage a more expansive view – one that recognizes translation not as an endpoint imposed from the outside, but as another powerful context in which discovery can thrive.

Curiosity and application are not opposing forces. They are, at their best, mutually reinforcing. And in a rapidly changing scientific landscape, learning to navigate and even embrace that interplay may be one of the most important skills that we can foster together.