Research Taste: The Art of Asking Questions Worth Pursuing

How do researchers learn to recognise questions worth pursuing? Reflections on curiosity, experiments, AI and helping PhD students develop independent scientific judgement.

Dandan Zhang

Multi-Scale Embodied Intelligence Lab, Imperial College London

One of the questions PhD students often bring to supervision is surprisingly simple: "My experiment is not working. What should I try next?"

There are usually several possible answers. We could change the model, collect more data, tune the parameters or redesign part of the experimental setup. With modern AI tools, generating potential solutions has become easier than ever.

But I sometimes wonder whether we are asking the right question.

Before deciding how to improve an experiment, perhaps we should ask why we are doing it in the first place. What exactly are we trying to understand? If the experiment succeeds, what will we have learnt? And if it fails, will the result still tell us something scientifically meaningful?

These are questions about what researchers sometimes call research taste.

Research taste is difficult to teach, even though I believe it is one of the most important qualities a scientist can develop. It is not simply the ability to come up with creative ideas, recognise fashionable research topics or predict which projects will lead to publications.

For me, research taste is the judgement to recognise which scientific problems are worth investigating, which observations deserve deeper attention and which directions may lead to meaningful discoveries.

In other words, it is not only about knowing how to solve a problem. It is about knowing which problems are worth solving.

A Technically Good Idea Is Not Always a Good Research Question

In robotics and artificial intelligence, there is no shortage of technically interesting problems.

We can develop a more accurate tactile sensor, design a more sophisticated neural network or improve the success rate of a manipulation policy. These are all legitimate research objectives.

However, I think we sometimes become so focused on how to improve a method that we forget to examine what the improvement actually means.

Consider a project on tactile perception.

Suppose a student develops a new learning model that achieves higher accuracy in estimating contact forces from tactile images. The result looks promising, and the student is naturally excited.

I would be interested too. But I would also want to understand what makes the method better.

Has the model learnt a more meaningful representation of physical contact? Does it capture deformation more reliably? Or has it become better at exploiting features specific to the sensor and experimental conditions?

What happens when we change the contact location, use a different sensor or introduce unfamiliar materials?

These questions are not intended to make the student's achievement seem less valuable. They help us understand its scientific significance.

Perhaps the most interesting contribution is not another improvement in prediction accuracy, but a deeper understanding of how tactile information depends on physical embodiment and sensing mechanisms.

This is a recurring theme in my own research on multi-scale embodied intelligence. I am interested not only in building systems that perform well, but also in understanding why they work, where their capabilities come from and under what conditions they fail.

A similar distinction arises in microrobotics.

Suppose a microrobot cannot manipulate a target reliably. We could develop a better controller, improve localisation or refine the actuation system.

But what if the real limitation lies in the robot's physical configuration?

At microscopic scales, geometry, material properties and interactions with the surrounding environment can fundamentally influence what a robot can achieve. A control strategy may compensate for some limitations, but not necessarily all of them.

This leads to a question that I find particularly interesting: when is it sufficient to adapt the control strategy, and when must we change the physical embodiment itself?

Rather than pursuing an endless sequence of control improvements, we might investigate the relationship between physical configuration, environmental conditions and achievable capabilities.

That is a different kind of scientific problem.

The distinction is not between engineering and science, or between incremental and ambitious work. Good engineering can reveal fundamental scientific principles, and seemingly modest technical improvements can open important new directions.

The more useful distinction is between improving something because we can and investigating something because we have a compelling reason to believe the result will matter.

Good Research Taste Requires Knowing What Not to Do

There is another side to research taste that I think deserves more attention: the ability to decide which ideas not to pursue.

Research time is limited. Students have finite resources, experiments can be expensive, and even a seemingly straightforward project may require months of development.

An interesting idea is not necessarily a good project.

Some problems are scientifically important but currently beyond our experimental capabilities. Others are feasible but offer limited potential for new understanding. Some require complex technical development before we can even test the central hypothesis.

A researcher needs to recognise these differences.

I do not think we should avoid difficult or high-risk problems. Quite the opposite. Many important scientific advances begin with questions that initially appear challenging.

But ambition should be accompanied by judgement.

For example, before committing several months to developing a complex learning architecture, could we first conduct a simpler experiment to establish whether the underlying hypothesis is plausible?

Could a carefully designed comparison reveal whether the limitation lies in sensing, control or hardware?

What is the smallest experiment that would genuinely change our understanding?

I find this last question particularly useful.

A large experiment is not necessarily more informative than a small one. Sometimes a simple, well-controlled experiment can eliminate several misleading explanations and prevent months of effort in the wrong direction.

Good research taste is not about always choosing the most complicated or ambitious idea. It is about recognising which investigation is likely to produce the most meaningful understanding.

And that requires knowing when to stop, when to change direction and when an unexpected observation deserves further attention.

Curiosity Is the Starting Point

I do not believe good research taste can be developed simply by reading more papers.

Reading is essential, of course. Students need to understand what has already been established, which methods are available and where important uncertainties remain.

But a comprehensive literature review does not automatically lead to an original research question.

A student may read hundreds of papers and still struggle to explain what genuinely interests them.

I think curiosity is often the missing ingredient.

Why does a tactile representation transfer well between some sensors but not others? Why can a manipulation policy succeed on unfamiliar objects yet fail when friction changes? Why does a microrobot behave differently near a boundary, even when the applied control signal remains unchanged?

These questions may begin with relatively small observations.

The important step is learning to recognise that an observation might reveal something more fundamental.

As supervisors, we should encourage students to notice such discrepancies and become curious about their causes.

When a student encounters an unexpected result, I would rather begin by discussing what might explain it than immediately telling them how to eliminate the problem.

Is the original assumption incorrect? Are we missing an important physical interaction? Could the experiment be measuring something different from what we intended?

Not every unexpected result contains a discovery. Sometimes the explanation is an ordinary calibration error or a software bug.

But learning to distinguish an interesting scientific problem from a routine technical difficulty is itself part of developing research taste.

Students should not feel that an idea is unworthy of discussion simply because they cannot yet explain it completely.

An uncertain observation, examined carefully, may be the beginning of an original research direction.

How Can We Teach Research Taste?

This is where I think the role of a PhD supervisor becomes particularly important.

It is relatively straightforward to teach students how to implement a method, explain an algorithm or recommend relevant literature.

Teaching someone to recognise a good scientific question is much harder.

I do not think research taste can be transferred directly from a supervisor to a student. Nor should the objective be to make students share all of their supervisor's preferences.

Instead, we need to make the process of scientific judgement more visible.

When discussing a research proposal, I would like students to understand why I find certain questions interesting and others less convincing.

Is the proposed problem genuinely unresolved? Does it challenge an important assumption? Is there a plausible way to investigate it? Would the result matter beyond the particular experimental setup?

I also want students to develop their own answers to these questions.

One approach I find useful is to ask students to compare several possible research directions rather than immediately settle on one.

Suppose a student wants to improve robotic manipulation under uncertain contact.

They might propose improving tactile sensing, developing an adaptive controller or changing the physical design of the gripper.

Instead of simply selecting a preferred solution, we can discuss what scientific assumptions each direction makes.

What evidence suggests that perception is the limiting factor? Could better control compensate for the uncertainty? Is there a physical capability boundary that neither approach can overcome?

The goal is not necessarily to reach an immediate answer. It is to help the student learn how to frame the problem.

I also think it is important to explain our own uncertainty as supervisors.

An experienced researcher may have a strong intuition about which direction is promising, but intuition is not infallible. We should be prepared to explain the reasoning behind our judgement and revise it when evidence suggests otherwise.

A student who always agrees with the supervisor may become efficient at following instructions. That does not necessarily mean they are developing independent scientific judgement.

I would much rather a student challenge my preferred approach with a well-reasoned alternative.

The ability to defend a scientific choice matters more than choosing the answer the supervisor expects.

Research Taste in the Age of AI

AI makes this discussion particularly timely.

A student can now ask a language model to generate ten novel research ideas, compare their potential significance and produce detailed experimental plans.

Some suggestions may be genuinely useful. AI can help us connect unfamiliar concepts, explore alternative approaches and identify possibilities that we might otherwise overlook.

Recent research suggests that the relationship between AI and scientific originality is more complicated than simply treating AI as either creative or uncreative.

For example, a study presented at ICLR 2025 found that AI-generated research ideas were judged more novel than ideas proposed by human researchers, although they were rated slightly less feasible. More recent studies have also raised questions about how AI influences the diversity of scientific research and how researchers evaluate AI-generated suggestions.

These findings reinforce an important distinction: originality, feasibility and scientific significance are related, but they are not interchangeable.

A proposal can sound original without being genuinely valuable. It can appear technically sophisticated while addressing a poorly defined problem. It can contain an elaborate experimental plan that does not actually test its central hypothesis.

AI is particularly effective at producing plausible explanations. That makes it easy to mistake a convincing research narrative for a sound scientific argument.

I do not want students to reject AI-generated ideas simply because they come from AI. That would be as unreasonable as accepting them without question.

Instead, I want them to develop the judgement to evaluate those ideas independently.

What is the actual scientific question? Has it already been investigated? Which assumptions are questionable? What evidence could distinguish the proposed explanation from competing alternatives?

And perhaps most importantly: why do you think this question deserves investigation?

I think the value of research taste increases when generating technically plausible solutions becomes easier.

If everyone can quickly generate research proposals, the ability to recognise which ones are meaningful becomes a more important part of scientific work.

AI may make it easier to explore a larger number of ideas. It does not remove our responsibility to decide which ideas deserve serious scientific attention.

Developing Your Own Scientific Judgement

There is a final point I consider especially important in doctoral education.

Students should not be trained simply to reproduce their supervisor's research taste.

Every scientist brings different experiences, interests and intuitions to a problem. What I find exciting may not be what a student eventually chooses to investigate.

That difference can be productive.

A student may notice a question I have overlooked or connect ideas from two fields in a way that would not have occurred to me. If I insist that every research direction must follow my initial judgement, I may unintentionally limit the student's originality.

My responsibility is to help students examine their ideas critically, understand their scientific significance and develop realistic ways of investigating them.

This requires more than giving them freedom. Students need constructive feedback, access to resources, technical guidance when necessary and a research environment where they can raise uncertain ideas without fear of being dismissed.

Independence develops through supported practice, not by leaving students to work everything out alone.

As students gain experience, I hope they gradually become less dependent on my judgement. They should be able to recognise promising questions, explain why those questions matter and make informed decisions about which directions to pursue.

Eventually, I would like them to develop research interests and scientific perspectives that are distinctly their own.

To me, that is one of the most meaningful outcomes of PhD supervision.

Learning to Recognise What Matters

Scientific research will always involve uncertainty. We cannot know in advance which experiments will succeed, which hypotheses will survive or which ideas will eventually become important.

Good research taste does not eliminate that uncertainty.

It helps us make thoughtful decisions within it.

I hope my students will learn to be curious about unexpected observations, sceptical of convenient explanations and willing to investigate difficult questions when there is a compelling scientific reason to do so.

I also hope they will learn that not every improvement needs to become a paper, not every fashionable direction deserves their attention and not every unsuccessful experiment represents wasted effort.

The most valuable contribution may sometimes come from recognising that the problem everyone is trying to solve has been framed incorrectly.

As AI continues to transform scientific research, I believe we should spend less time training students merely to produce more ideas and more time helping them develop the judgement to recognise which ideas matter.

Knowing how to solve a problem makes someone a capable researcher. Learning to recognise which problems are worth solving is an important part of becoming an independent scientist.

---

Further Reading: Research Taste and Scientific Creativity in the AI Era (2025–2026)

1. Peters, M. A. K. (2025). How to Develop Good Research Questions. Nature Human Behaviour, 9, 1759–1761.

A particularly relevant article on developing scientific questions through creative reframing, challenging assumptions and recognising limitations in established methods. I recommend this as the first reading for PhD students.

2. Si, C., Yang, D. and Hashimoto, T. (2025). Can LLMs Generate Novel Research Ideas? A Large-Scale Human Study with 100+ NLP Researchers. International Conference on Learning Representations (ICLR 2025).

A human evaluation of AI-generated research ideas. The study found higher perceived novelty for AI-generated ideas, alongside somewhat weaker feasibility and limitations in idea diversity and AI self-evaluation. It provides evidence for distinguishing idea generation from research judgement.

3. Hao, Q. et al. (2026). Artificial Intelligence Tools Expand Scientists' Impact but Contract Science's Focus. Nature, 649, 1237–1243.

A large-scale study showing an association between AI use and increased individual research productivity, alongside a narrowing of the scientific topics pursued collectively. It raises an important question about whether improving research efficiency necessarily produces broader scientific exploration.

4. Tröbinger, M., Doshi, A. R. and Chai, S. (2026). How Experience Moderates the Impact of AI Suggestions on Researchers' Perceptions of Their Ideas. Research Policy, 55(8), 105575.

An experimental study investigating how researchers with different levels of experience respond to AI-generated suggestions. It found that less experienced researchers were more inclined to incorporate such suggestions. This is directly relevant to training doctoral researchers to develop independent judgement.

5. Machado, D. (2026). Generative AI Bias Against Scientific Novelty: A Cautionary Tale from a Small-Sample Evaluation of Research Proposals. Scientometrics, 131, 7479–7497.

An exploratory study of 139 research proposals comparing AI-based funding decisions with human review outcomes. Its findings suggest a possible tendency for the tested AI system to undervalue proposals assessed as highly novel by human reviewers. The limited sample and model configuration mean the finding should not be generalised to all AI systems.

6. Payne, D. (2026). Is AI Eroding PhD Students' Critical Thinking and Analysis Skills?. Nature Careers, 15 October 2026.

A recent panel discussion examining how AI is changing doctoral education, particularly the need to preserve critical reasoning, analytical skills and intellectual ownership.

These readings provide research evidence and contemporary perspectives. The arguments and proposed supervision philosophy in this article remain my own interpretation.

Conceptual illustrations

The illustrations below were generated with AI. They are conceptual and do not document actual people, events or experimental results.

Conceptual illustration generated with AI; it does not depict actual individuals, events or experimental results.