Scientific papers are becoming increasingly complex, often containing multiple omics datasets, a variety of model organisms, and substantial computational wizardry. But here's an uncomfortable question: Do we actually understand biology any deeper, or are we unnecessarily getting lost with a super-powerful lens we are not yet ready to interpret fully?
I've been watching an alarming trend unfold over the past few years as a reader, as a referee, and regrettably, as an author myself (even though I try to restrain!). Fifteen years ago, a paper in a top-tier journal might have contained 4 main figures and a similar number of supplementary ones, each with a reasonable number of panels. We could actually read and understand these papers in one sitting.
Fast forward to today. Main figures? Usually 5 or 6. Supplementary figures? Easily 10 to 15. And that's before we get to the "additional supplementary figures" that journals now accommodate because apparently, regular supplementary figures weren't enough. Each figure now shows so many panels that it needs the entire English alphabet (yes, the one with all the letters). What's emerged is a kind of "brute force science" that flexes methodological muscle more than it clarifies ideas. It equates volume with validity and scale with understanding.
But it's not just the quantity. Each figure is now an overwhelming assemblage of data thrown at the reader: multiple omics datasets stitched together, a variety of model organisms spanning evolutionary distances (because we must prove evolutionary conservation, naturally), and enough computational "integration" to make your head spin. The kicker? Out of this enormous complexity emerges a remarkably simple, linear mechanism usually captured perfectly in a beautiful graphical abstract. Even more remarkably, this linear process, when blocked, apparently cures cancer, reverses neurodegeneration, or stops ageing. The effect is to overload editors and reviewers to the point where rejection becomes psychologically and politically costly: who dares dismiss a paper with a budget befitting a small country and 70 supplementary panels? It must be good.
Yet somehow, many of these findings struggle to translate into practical application. Instead, many of these gigantic papers become "resources": costly, sprawling datasets that impress by mass more than by insight, confounding readers and reviewers while rarely guiding action. We're left with warehouses of measurements and too few ideas.
What is going on? This is not really about the reproducibility crisis, though that's certainly part of it. The issue is deeper and more insidious: We've entered a hypothesis crisis. We're forgetting how hypotheses are generated, replacing that craft with spectacle and volume, which usually guarantees a place in a journal.
The current trend is clear: papers are increasingly driven by the experimental approaches employed rather than the biological questions they're supposed to answer. You can see this in the titles themselves: papers now advertise their multi-omics methodology front and centre, with the actual biological insight buried somewhere in the fine print (and the graphical abstract, of course!). This is the brutalism of science: questions subordinated to toolkits, insight drowned by inventory, and authors becoming compulsive professional generators of "resources" rather than builders and breakers of hypotheses. In this mindset, AI becomes a talisman: pattern-finding is mistaken for explanation, and prediction is mistaken for understanding.
The story goes like this:
Step 1: Collect a bunch of expensive (the pricier, the more likely editors will notice) multi-omics datasets on some biological condition. Not because you have a specific hypothesis about what you'll find, just because you can, and because that's what reviewers expect (not me, though!).
Step 2: Generate a tsunami of volcano plots (at best, more complicated visualisations are waiting!). Drown your readers in them. Make sure there are so many differentially expressed/modified/methylated features that nobody could possibly digest them all.
Step 3: From this overwhelming chaos, cherry-pick some promising dots. (Don't worry, there's always an appropriate statistical strategy to support whatever selection you make.)
Step 4: Watch as a biological pathway magically appears! It was there all along, waiting to be discovered.
Step 5: Enter the "validation" phase. Pick your favourite regulation mechanism: these days, it's either an epigenetic modification or a post-translational modification somewhere along the line. Generate every mutant under the sun to "prove" your point.
Step 6: Build a new mouse model of the disease. Demonstrate that your axis works "in vivo." Declare translational relevance.
Step 7: Submit to your target journal.
Is there anything technically wrong with this procedure? Not if the results are valid and reproducible. But conceptually, this approach has several devastating implications.
Hypothesis Retrofitting
Scientists, in a desperate scramble to publish, apply every omics approach imaginable, hoping something valuable will emerge and hoping the data itself will provide the narrative. This is HARKing (Hypothesising After Results are Known) on an industrial scale. The hypothesis isn't driving the research. It's being reverse-engineered from the data. The scientific discovery is an actual byproduct of a virtuoso data collection, a narrative sculpted after the fact by statistical machinery and, increasingly, by black-box models.
The Needle-in-Haystack Delusion
When you identify your favourite "axis" from among thousands of changes, you're committing a cardinal sin: oversimplification. We're studying incredibly complex biological systems, then pointing to one pathway among thousands and saying, "This is the mechanism." It's not intellectual honesty; it's intellectual convenience. We're relying more on statistical significance than biological significance, and in the worst cases, we might just be analysing reproducible biological noise.
The PTM Problem
Let me be specific about one example: post-translational modifications (PTMs).
Modern proteomics is so sensitive that you can detect almost any PTM if you look hard enough. Need a metabolite-driven modification event to close your story? You'll find one. Need ubiquitination? It's there. Acetylation? Methylation? Take your pick. Validation typically involves creating point mutations that block or mimic the PTM. But here's the question nobody asks: If the PTM you detected affects only 0.5% of the protein population, does your overexpression mutant tell you anything meaningful about the endogenous biological function? We're treating detection as significance. They're not the same thing.
To be fair, this isn't universally true. There are exemplary cases in which comprehensive multi-omics approaches have genuinely advanced our understanding, for instance, by identifying unexpected disease mechanisms or revealing systems-level principles that single-method studies would have missed. When hypothesis-driven questions guide the experimental design from the outset, these powerful tools can be transformative. The problem isn't the technology itself; it's the increasingly common practice of letting the technology drive the questions.
This isn't just an academic complaint about methodology. This trend has real consequences: The omics arms race creates a two-tier system. Labs with substantial funding can afford the "omics of the month." Labs without that funding are locked out of competitive publishing. Science becomes plutocratic rather than meritocratic. Nothing new though!
We're generating data faster than we can interpret it. And now, with AI entering the picture as a "hypothesis generator," we risk amplifying this problem rather than solving it. AI trained on these massive, noisy datasets will churn out more hypotheses, which will demand more omics, which will feed more AI...for the sake of it. The cycle accelerates. The human scientist becomes increasingly marginalised. We are forgetting why we do science. If you are familiar with Marx's term alienation, you know this is exactly what happens in a capitalist society. In this case, we are in a full-blown science-capitalism phase, with alienated scientists mistaking the process (data collection) for the goal.
I strongly believe we need to reposition the scientist at the centre of the hypothesis-generating process. We should exploit omics and computational tools, not be enslaved by them. We are the observers and interpreters of reality. By outsourcing hypothesis generation to our tools, we risk losing the uniquely human perspective that makes science creative, insightful, and meaningful. We're mistaking the means for the end. We need to truly learn the art of hypothesising again.
What might this look like in practice? Start with a genuine biological puzzle, an observation that doesn't fit current models. Formulate a specific, testable hypothesis before touching any high-throughput platform. Use omics strategically, as targeted tools to answer particular questions, not as exploratory fishing expeditions. Insist that every dataset in your paper serves a clear purpose in testing your hypothesis, not just demonstrating technical capability. And perhaps most importantly, recognize that a paper with three well-justified figures can advance understanding more than one with thirty that exhaust attention.
This is a conversation worth having, and one I'll continue exploring. But for now, the challenge is clear: reclaim the hypothesis as the heart of scientific inquiry.