If paired biopsy is this noisy, how do MASH trials detect anything at all?

Following on from the discussion of sampling variability: if simultaneous biopsies from the same liver disagree by a fibrosis stage in a meaningful fraction of cases, and if ballooning has only moderate inter-observer agreement, then the measurement error on the primary endpoint of every MASH trial is large. I would expect that to make these trials hopeless.

Yet they do detect effects, sometimes with substantial separations - resolution rates in the sixties against placebo in the thirties. I would like to understand how that is possible. Is the noise smaller than I am imagining, does randomisation handle it in some way I am not seeing, or are the effect sizes simply big enough to survive it?

And a design question: given all of this, what would you actually change about how these trials are run? I have seen suggestions about central reading, artificial-intelligence-assisted scoring, and continuous rather than categorical endpoints, and I cannot tell which of those addresses the real problem.

Randomisation handles it, but only in a specific way, and understanding which way tells you exactly which design fixes help.

Why the trials work

The critical property is that biopsy noise is non-differential: sampling variability and reader disagreement do not know which arm a participant is in, provided readers are blinded. Non-differential measurement error on a binary outcome does not bias the comparison towards a false positive. It does two other things:

• It attenuates the observed effect towards the null. Some true responders get scored as non-responders and vice versa, and because misclassification acts in both arms it compresses the between-arm difference. So the true effect of these drugs on histology is probably larger than the reported difference, not smaller.
• It inflates the variance, so it costs power. This is why MASH trials need hundreds of participants to detect effects that would need dozens with a clean endpoint, and why they take 72 weeks and cost what they cost.

So the answer to "how do they detect anything" is: the effects are large, the trials are large enough to absorb the attenuation, and the direction of bias from the noise is conservative. What you should not conclude is that noise explains the placebo response - it explains the placebo response rate being high in absolute terms, but not any between-arm difference.

The one place noise becomes dangerous is where it stops being non-differential:

• If readers are unblinded to timepoint, they see a sequence and expectations creep in.
• If biopsy adequacy differs between arms - for example if one arm has more dropouts and their end-of-study biopsies are missing - then missingness is differential even though the reading is not.
• If baseline biopsy is used for enrolment eligibility and re-read later, regression to the mean operates on the enrolled sample. Participants enrolled on a borderline-high activity score will on average score lower at re-read regardless of treatment. This is a substantial contributor to the placebo resolution rate and it is a selection artefact rather than a reading artefact.

What to change, ranked by how much it addresses the real problem

1. Continuous or ordinal endpoints instead of dichotomised ones. This is the biggest win and the most under-used. Dichotomising a noisy ordinal score throws away information and puts all the statistical weight on whether a participant crossed one arbitrary boundary. Analysing fibrosis stage change as ordinal, or using a continuous morphometric measure of collagen area, recovers a great deal of power from exactly the same biopsies.
2. Central reading with multiple blinded readers and adjudication. Directly reduces the reader-variability component, which is the larger of the two noise sources for activity scoring. Already standard in good trials; still worth verifying rather than assuming.
3. Machine-assisted quantitative histology. Promising specifically because it converts categorical scoring into continuous measurement, which is really fix number one wearing different clothes. Its value depends on validation against outcomes, not against human readers - a system trained to reproduce human scores inherits human noise.
4. Better sampling. Longer cores, or two passes. Addresses the sampling component but is limited by what is ethical and tolerable, and it does nothing for reader variability.
5. Replacing biopsy with validated non-invasive markers. The long-term answer, and the one everyone wants. Blocked by the fact that qualifying a surrogate requires demonstrating it predicts clinical outcomes, which requires long trials with clinical outcomes - the thing biopsy endpoints were adopted to avoid.

The practical reader's checklist

When a MASH trial reports a histological result, look for: whether readers were blinded to treatment and to timepoint; how many readers and how disagreements were resolved; the biopsy adequacy criteria and how many were excluded; the proportion with an evaluable paired biopsy in each arm; and whether an ordinal or continuous analysis was reported alongside the dichotomised primary. A paper that reports all five is telling you it took the measurement problem seriously. Most of the major programmes in this space do report them, in the supplement [1].

Worth quantifying the power cost, because it makes concrete why this field moves so slowly.

Take a trial powered to detect a difference in resolution rates of 60% against 35%. With a perfectly measured endpoint, roughly 60 to 70 participants per arm would give conventional power. Now introduce misclassification in both directions - suppose 15% of true responders are scored non-responders and 15% of true non-responders scored responders. The observed rates compress: the 60% arm is observed at 0.60 x 0.85 + 0.40 x 0.15 = 0.51 + 0.06 = 0.57, and the 35% arm at 0.35 x 0.85 + 0.65 x 0.15 = 0.2975 + 0.0975 = 0.395. So a true 25-point separation is observed as about 17.5 points.

Required sample size scales roughly with the inverse square of the detectable difference, so the ratio is about (25 / 17.5)^2 = 2.04. The trial needs roughly twice as many participants for the same power, purely because of the misclassification. Add dropout, add biopsy refusal at the end of study, add inadequate samples, and the practical multiplier is larger.

Two things follow. First, the size of these trials is not padding, it is arithmetic. Second, this is exactly why the ordinal-and-continuous-endpoint argument in the accepted answer matters so much: it recovers power without recruiting anybody, which in a field where each participant needs two liver biopsies is worth more than in almost any other therapeutic area.

The misclassification rates used above are illustrative round numbers chosen to make the arithmetic legible, not measured values from any specific trial. The published reliability work suggests they are the right order of magnitude for activity scoring and possibly conservative for ballooning specifically.

One addition on the biopsy refusal problem, which is a differential-missingness risk and therefore the dangerous kind.

End-of-study biopsy is voluntary, invasive and unpleasant. Participants who feel worse, who have gained weight, or who are experiencing adverse effects are plausibly less willing to submit to a second biopsy than participants who feel they are improving. If that willingness differs between arms - and there is no reason it should not, given very different tolerability and weight trajectories - then the evaluable paired-biopsy population is a non-random subset of the randomised population, and the difference in selection between arms is not corrected by randomisation.

The direction is not predictable in advance. An active arm with high nausea might lose the least-well-tolerated participants, who could be either responders or not. A placebo arm might lose the disappointed, who are disproportionately non-responders, which would inflate the placebo response rate.

What to look for: the CONSORT flow diagram, specifically how many randomised participants contributed an evaluable end-of-study biopsy in each arm, and whether the primary analysis imputed missing biopsies as non-response. Imputing missing as non-response is the conservative convention and it is what most of the major programmes do, which is worth knowing because it means the reported rates are deliberately pessimistic in both arms. A paper that analyses only participants with paired biopsies, without a sensitivity analysis, is one to read more sceptically.