More hypotheses do not automatically mean more biology explored.
Imagine your agent returns ten promising targets for fibrosis. Each comes with a mechanism, supporting papers, and an experiment to run next. It looks like a useful afternoon’s work.
Now imagine another biotech asking the same model a similar question, with access to the same public databases. How much of its shortlist would overlap with yours?
That is the question I think deserves more attention as research agents enter biology. Ideas are getting cheaper. Experiments remain expensive. If we spend that experimental budget testing variations of the same familiar hypotheses, faster idea generation only gets us so far.
A good answer can come from a narrow pool
A Stanford study generated 4,000 research ideas per topic in natural language processing. After deduplication using the authors’ similarity measure, about 200 distinct ideas remained per topic, on average. Further generation increasingly revisited ideas already proposed.1
Yet the same study found that selected AI ideas were rated more novel than ideas from human researchers. An agent can offer a compelling suggestion while producing a surprisingly repetitive collection of suggestions.
For a research team, both levels matter. You want each hypothesis to be credible. You also want the set to cover meaningfully different possibilities. Ten plausible targets are less informative if all ten depend on the same untested assumption.
Biology’s literature is an uneven map
In 2018, researchers studying scientific attention noted that most human gene research concentrated on roughly 2,000 of about 19,000 genes. Gene properties and knowledge of homologs in model organisms explained much of that attention. What gets studied reflects a history of experimental accessibility and accumulated knowledge, alongside disease relevance.2
That creates a problem worth watching as agents help nominate targets. A familiar gene comes with an abundance of mechanisms, assays, and citations. An understudied gene may be harder to build a convincing explanation around, even when an experiment gives you a reason to investigate it.
My concern is that we could mistake the ease of explaining a target for the strength of the case for pursuing it.
Scientists already have this tendency. Historical work on biomedical chemistry found a strong preference for revisiting established chemical relationships.3 AI gives us a way to reproduce familiar starting points much faster.
A 2026 Nature analysis of 41.3 million papers found a related tension: researchers using AI had higher publication and citation counts, while AI-associated work covered a narrower topical space. This was an observational study spanning multiple eras of AI, including traditional machine learning. It does not establish that current LLM agents cause labs to converge, but it gives us reason to question whether greater output necessarily means broader exploration.4
Give your agent a reason to reach a different conclusion
I would start with three changes to how a biotech team uses research agents.
1. Let different evidence shape the initial hypotheses.
Start one search from human genetics, another from perturbation results, and another from clinical observations. Let each develop its case independently before comparing the conclusions. Where they disagree, ask which assumptions or pieces of evidence account for the difference.
There is some support for deliberately varying starting perspectives. A Columbia Business School preprint found that diverse personas improved idea diversity, and combining them with structured reasoning prompts surpassed the human comparison on key diversity measures. Those experiments involved fitness-product ideas, so their application to biology still needs testing. But they show that prompting can widen a model’s search.5
For a scientific workflow, I would go further and vary the evidence itself. Giving three agents different job titles is a useful experiment; giving them different observations is a more direct test of whether those observations change the answer.
2. Make your own experimental history usable.
The evidence that changes a shortlist might already exist inside your team.
Suppose a target has strong literature support, but your own experiment showed no effect in the relevant cell type. That result needs context: was the perturbation effective? Was the assay sensitive enough? Did the effect disappear only under a particular condition?
Depending on those answers, the next step could be to abandon the hypothesis, repeat the measurement, or investigate why the context matters. A record that says only “no effect” cannot support that decision.
This is why I think experimental history belongs inside the hypothesis-generation workflow. Preserve the conditions, controls, unsuccessful attempts, and reasoning behind changes in direction. Connect them to the question the agent is being asked now.
Where the evidence is missing, design experiments to fill that gap. A new cohort, time point, or biological model is valuable when it resolves a specific uncertainty. Owning more data does not, by itself, make your conclusions better.
3. Evaluate the alternatives your shortlist preserves.
Compare your recommendations with a baseline built from public evidence alone. Then look beyond whether the gene names differ.
Do the hypotheses involve different mechanisms? Do they make different predictions? Would the proposed experiments distinguish between competing explanations? Which recommendations changed because of something your team learned?
Some agreement is exactly what you want: strong evidence should lead people toward similar conclusions. The useful test is whether your system can recognize a credible reason to reconsider them.
When your own data changes an agent’s answer, you should be able to see which evidence made the difference.
Everyone can read the same papers. What your team can add is the knowledge it earns by doing the work: the result that failed to replicate, the condition that changed an effect, the observation that made you reconsider a mechanism.
The advantage I would build toward is an agent that carries those lessons into the next experiment. When experiments are expensive, remembering what should change your mind matters as much as generating something new to try.
References
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Si C, Yang D, Hashimoto T. Can LLMs Generate Novel Research Ideas? A Large-Scale Human Study with 100+ NLP Researchers. ICLR (2025); preprint first posted in 2024. ↩
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Stoeger T, Gerlach M, Morimoto RI, Nunes Amaral LA. Large-scale investigation of the reasons why potentially important genes are ignored. PLOS Biology 16(9):e2006643 (2018). ↩
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Foster JG, Rzhetsky A, Evans JA. Tradition and Innovation in Scientists’ Research Strategies. American Sociological Review 80(5):875–908 (2015). Open preprint. ↩
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Hao Q, Xu F, Li Y, Evans J. Artificial intelligence tools expand scientists’ impact but contract science’s focus. Nature 649:1237–1243 (2026). Open author manuscript. ↩
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Deng Y, Brucks M, Toubia O. Examining and Addressing Barriers to Diversity in LLM-Generated Ideas. arXiv:2602.20408 (2026). Preprint. ↩