Causal inference across a single person's whole record

The problem

A person who wants to know whether something helps them has two unsatisfying options. They can read a randomised trial, which reports an average over people unlike them on an outcome they may not have chosen. Or they can try it and watch a dashboard, which shows correlations between everything and everything else.

Consider the evidence base for a supplement taken by millions. The most-cited synthesis of magnesium for insomnia pools three randomised trials covering 151 people, and grades the resulting evidence low to very low, with all three trials at moderate-to-high risk of bias [1]. It finds sleep onset latency falls by 17.36 minutes (95% CI −27.27 to −7.44) and that total sleep time changes by 16.06 minutes with an interval of −5.99 to +38.12 — consistent with a loss and with a substantial gain.

Suppose that estimate were solid. It would still be an average over a population defined by a diagnosis and an age band. Heterogeneity of treatment effect is not a caveat to that estimate; it is the entire question a person is asking when they wonder whether to keep taking something.

The case that motivated this

Baseline's founder spent years being treated for eczema. The treatment was topical throughout — successive steroid creams of escalating potency, each of which worked while applied and stopped working after. Every consultation took the symptom's location as the place to look. What eventually changed the trajectory was not a stronger cream but a change in diet, and with it a change in gut function.

That is one person, and it is worth being exact about what it does and does not show. It is not evidence that eczema is a gut condition. The literature describes an association between gut dysbiosis and atopic dermatitis — reduced microbial diversity, fewer short-chain-fatty-acid producers such as Bifidobacterium, more Clostridium difficile — while stating plainly that causation is unresolved and the evidence conflicting [2]. The direction is not settled either: dysbiosis may drive skin inflammation, or the reverse, or both may follow something else.

Symptoms and causes live in different domains

Medicine is organised by the site of the complaint. Skin goes to dermatology, gut to gastroenterology, sleep to a sleep clinic. That division is efficient when the cause is local, and structurally blind when it is not — a dermatologist running a perfect differential over skin findings will never surface a dietary cause, because dietary data was never in the frame.

The consequence for a data system is specific. If the record contains only the domain the symptom appears in, no estimator, however good, can recover a cause outside it. Absent data is not noise to be modelled around; it is a hypothesis that cannot be stated. This is why the ingestion problem comes before the inference problem in this paper, and why the record cannot have a fixed schema.

Why the dashboard fails

The second option fails structurally rather than for lack of data. A single person's history is short, serially correlated, and confounded by everything that varies alongside the intervention. Ordinary summaries over that history recover the confounders as readily as the effect.

More sensors do not fix this. They add dimensions to search, which makes spurious findings more likely rather than less. A system that reports every correlation it can compute will, given enough streams, always have something to show you.

One record

Because the cause may sit in any domain, the record accepts any stream a person can produce: wearables and rings, blood and urine panels, continuous glucose, stool and microbiome sequencing, food and drink logs, medications and topicals, symptom scores, menstrual cycle, air quality, travel, training load, mood, and anything else that arrives with a timestamp and a value. There is no fixed schema, because a fixed schema is a prior claim about where the answer is — and section 01 is the case against making that claim.

A new source needs three things to be usable: a timestamp, a value, and an honest statement of how it was measured. Given those, it joins the record without a code change. What it does not need is a hypothesis in advance about which outcome it might explain.

Streams arrive at incompatible resolutions. Wearables emit near-continuous signals; blood panels are drawn every few weeks; a microbiome sample might exist twice a year; meals and symptoms are logged irregularly and incompletely; a topical steroid is a protocol rather than a measurement. The first step is alignment onto a common daily index.

Each stream carries its own observation model rather than being interpolated into a shape it does not have. Sparse streams stay sparse: a panel drawn on night 3 informs neighbouring nights through the model, not through forward-filling, which would fabricate precision the measurement never had.

Measurement error is not a footnote

Consumer wearables report sleep stages as though they were measurements. They are inferences, typically from movement and cardiac signals, trained to approximate what a sleep laboratory would score from EEG. A 2025 validation of six wrist-worn devices against simultaneous polysomnography found overall stage agreement between κ = 0.53 and κ = 0.21, and deep-sleep bias ranging from −25.20 minutes to +44.44 minutes per night depending on the device [3].

That error is larger than most effects worth detecting. The reason n-of-1 estimation survives it is that a personal trial does not ask what your deep sleep is; it asks whether your deep sleep changed. Accuracy — closeness to truth — matters for the first question. Reliability — an error that stays put — matters for the second. A device that overstates deep sleep by half an hour every night contributes that offset to both arms of a within-person contrast, where it largely cancels.

The cost of searching everywhere

Accepting arbitrary streams buys the ability to find a cause outside the symptom's domain. It also creates the failure the dashboard already has, at larger scale: the more streams in the record, the more candidate explanations, and the more chances for one to look convincing by accident. Widening the search without paying for it is how a system ends up confidently telling someone their sleep improved because of a supplement they happened to start in the same week they stopped travelling.

This is the honest cost of the previous section, and it has to be paid explicitly rather than hoped away. Four mechanisms do that.

Separate the two questions

Searching the record for candidate relationships and estimating an effect are different operations with different standards, and conflating them is what produces confident nonsense. Exploration over the full record is allowed to be liberal — its output is a ranked list of hypotheses, not a set of results, and it is labelled that way. Nothing from that stage is reported as an effect.

A relationship becomes a candidate for estimation only when it is named in advance of the data used to test it. In practice that means a hypothesis surfaced by exploration is tested against a held-out period, or against data collected after the hypothesis was written down. The same data cannot both generate and confirm.

Shrink everything toward no effect

The hierarchical model in section 04 does the statistical work here. Because each candidate effect is drawn from a population distribution centred near zero, a relationship supported by little data is pulled toward no effect rather than reported at its noisy face value. Searching more streams therefore does not proportionally increase the number of confident findings — it increases the number of wide, uncommitted posteriors, which is the correct response to a wider search.

Report the denominator

A result means something different when it was the only thing tested than when it was the most striking of two hundred. Every reported effect carries the size of the search it came from, so a reader can discount it appropriately. A system that hides its denominator is not reporting a result; it is reporting a selection.

Require a protocol to confirm

For anything actionable, the observational finding is treated as a hypothesis and the protocol in section 06 is what settles it. This is the strongest of the four, because a randomised on/off schedule breaks the confounding that generated the spurious candidate in the first place. It is also the slowest, which is why it is reserved for findings a person intends to act on.

How the model works

The estimator is a hierarchical Bayesian time-series model fitted to each person's own record, with parameters partially pooled across a cohort. The mechanics matter less here than the property they produce, so this section describes what the model does rather than how it is specified.

The question it answers is narrow and personal: given this individual's history, how much did this intervention move this outcome, and how sure can anyone be? The output is that person's own effect, not the cohort average. The cohort enters only as an answer to a prior question — before seeing your data, what is a plausible size for an effect like this? — and that prior is then updated by your record.

Three things the model has to handle at once, none of which a correlation can:

• ·Serial dependence — tonight resembles last night, so sixty nights carry far less information than sixty independent measurements.
• ·Confounders that move with the intervention — travel, alcohol, illness, season — which are modelled as competing explanations rather than filtered out.
• ·Measurement error that differs by stream — a wearable's inferred sleep stage and a laboratory blood panel are not equally trustworthy, and the model should not treat them as though they were.

Partial pooling

Because a person's effect is modelled as drawn from a population distribution rather than estimated in isolation, the estimate adapts to how much a person's own data can support. Where their record is short or noisy, the estimate shrinks toward the cohort; where it is long and clean, it stays close to what their record says. This is the component that does the most work, and removing it costs more accuracy than removing any single data stream.

The approach is established for aggregating series of n-of-1 trials rather than invented for consumer health. Zucker, Ruthazer and Schmid worked through the modelling choices on n-of-1 trials of amitriptyline and a combination therapy, and found the best-fitting specification paired a random intercept — each patient's own baseline response — with a fixed treatment effect [4].

Where it breaks

The same work is direct about the failure mode: hierarchical Bayesian models improved precision, but were highly sensitive to the priors placed on within-patient variance [4]. That sensitivity is not a technicality. The within-patient variance prior governs how much of a person's night-to-night variation the model attributes to noise, and therefore how hard it pulls their estimate toward the cohort. Choose it carelessly and you can manufacture a confident personal result that is largely an echo of the population.

The response is unglamorous: state the priors, refit under alternatives, and report when the posterior moves. A result that survives only under one convenient prior is not reported as a result.

Confounding and carryover

Known time-varying confounders enter the model explicitly as covariates rather than being filtered out of the data:

• ·Travel and time-zone displacement
• ·Alcohol, dose and timing
• ·Meal timing relative to sleep onset
• ·Acute illness
• ·Menstrual phase, where applicable

Modelling them rather than excluding them means a night on protocol that also involved a late meal contributes what it can, instead of being discarded and shrinking an already short series.

Carryover

An intervention whose effect persists after it stops will contaminate the following off-protocol period and bias the contrast toward zero. The conventional remedy is a washout period between treatment periods, long enough for the person to return to baseline [5].

Washout is not always available or ethical, and it costs time in a design that is already short of it. The alternative is analytic: discard or downweight observations taken at the start of a new period, which achieves the same end without withholding anything [5]. Baseline downweights rather than discards, on a decay whose length is set per intervention class.

Design

How a trial is arranged matters as much as how it is analysed, because serial correlation destroys power. In simulations of n-of-1 crossover designs, power to detect a 0.3 SD difference fell from 0.851 with independent observations to 0.126 once serial correlation reached ρ = 0.75 [6].

More cycles, not more nights

The same work shows the remedy, and it is counter-intuitive: holding the total number of observations fixed at 400 and simply breaking them into more, shorter alternating periods recovered most of the lost power. At ρ = 0.75, a single-period design achieved 0.126; a forty-period design achieved 0.681 [6]. Same data, same duration, five-fold difference — purely from how the periods were arranged.

This is why protocols are specified as repeated short cycles with randomised start rather than one long on-block followed by one long off-block. The second arrangement is easier to adhere to and much worse at answering the question.

Sizing

A protocol is sized to a target interval width rather than to a significance threshold. The person sets how precise an answer would have to be to change what they do; the design is then chosen so the expected posterior width at completion falls below it. This gives a completion date instead of an open-ended commitment, and it makes the trade-off explicit: a narrower interval costs more nights.

Reporting

Every result is reported as three numbers: the effect size, a 95% credible interval, and the posterior probability that the effect is beneficial. There is no significance threshold.

The American Statistical Association's 2016 statement is unusually direct about why a threshold cannot carry the weight placed on it: “a p-value, or statistical significance, does not measure the size of an effect or the importance of a result”, and “smaller p-values do not necessarily imply the presence of larger or more important effects, and larger p-values do not imply a lack of importance or even lack of effect” [7].

Return to the magnesium result in section 01. Total sleep time changed by 16.06 minutes, interval −5.99 to +38.12, p = 0.15. Under a threshold rule that becomes four words — no significant effect — which is compatible with the data and discards what the reader needed. The interval says the evidence spans a small loss and a substantial gain. Someone deciding whether to keep taking a capsule every night is entitled to know the range is that wide.

Credible, not confidence

A confidence interval is a statement about a procedure: intervals constructed this way would contain the true value 95% of the time across repeated experiments. A credible interval is a statement about the parameter: given this data and these priors, there is a 95% probability the effect lies in this range. The second is what people already assume the first means, and it is the question being asked about one's own body.

The cost is the headline. We cannot report that something works. We report that the estimate is +18 minutes a night, that the plausible range runs +6 to +31, and that the posterior probability of benefit is 97%.

Abstention

When the posterior is too wide to act on, the system reports that the question has not settled rather than selecting the nearest verdict. An interval spanning zero is a result: it says the data are consistent with no effect and with a meaningful one, and quantifies how much of each remains plausible.

Abstention is only useful if it comes with a route forward. Each unsettled result is paired with the protocol that would settle it — cycle structure, randomised start, expected interval width at completion, and the confounders to be held — so that an inconclusive answer becomes a plan with a date rather than an open question.

N1Bench, and why we published it

Every claim in this paper is checkable in principle and unfalsifiable in practice unless someone measures it. There was no benchmark for causal reasoning over personal health records, so we built one and made it open rather than keeping it internal.

N1Bench scores a system on held-out records with planted ground truth — records where the true effect is known because it was constructed, so an answer can be graded rather than argued about. Three things are measured:

• ·Effect recovery — how close the recovered effect is to truth, normalised by the outcome's own night-to-night variation.
• ·Calibration — whether a stated 95% interval contains the truth 95% of the time. Overconfidence and uselessly wide intervals are penalised equally, so a system cannot score well by hedging.
• ·Abstention — on records where no effect was planted, how often the system declines to find one.

Abstention is the metric that matters

The first two are the obvious ones and the third is the one that separates systems. A model that always produces a confident answer will look competent on any dataset where an effect exists, and will invent effects everywhere one does not. Nothing in a demo reveals this. Only records with a known-absent effect do.

This is also the metric where a general-purpose language model reasoning over a health record does least well, and it is the reason the benchmark is worth having independent of who wins it. A field optimising only for finding things will build systems that find things that are not there.

Publishing our own scores

We publish our results next to every system we test, including where we lose. A company that both builds the benchmark and competes on it has an obvious incentive problem, and the only workable answer is to make the records, the harness, and the scoring open enough that anyone can rerun them and dispute the result.

The intent is that the benchmark outlives our use of it. If a better method appears and beats us on our own measure, the field has moved, which is the point of publishing rather than the failure of it.

Individual write-ups follow CENT 2015, the CONSORT extension for n-of-1 trials, which provides additional guidance for 14 of the 25 items on the CONSORT 2010 checklist [8]. It exists because n-of-1 designs have historically been reported too thinly for readers to judge validity or reproduce what worked, which is why our results carry period structure, randomisation detail, and washout alongside the effect size.

Building models for this problem

General-purpose models are strong at reading a record and weak at the specific thing this problem demands. Asked whether an intervention worked, they tend to produce a fluent, plausible, confident answer — which is the failure mode this entire paper is organised against. The gap is not knowledge. It is calibration, and a willingness to return nothing.

So the work splits in two. The statistical estimator does what statistics does well: quantify an effect and its uncertainty from sparse, correlated, confounded data. A model does what statistics cannot: read an irregular human record, work out which of two hundred streams are even plausible candidates, know that a topical steroid and a dietary change are different kinds of intervention, and turn a posterior into something a person can act on without overstating it.

What we are training for

• ·Knowing when to abstain — the hardest behaviour to train, because every incentive in a helpful assistant pushes the other way.
• ·Proposing hypotheses across domains, so a skin question can surface a dietary candidate rather than only dermatological ones.
• ·Reading heterogeneous records — irregular, incomplete, and inconsistently measured — without silently imputing what is missing.
• ·Designing the protocol that would settle a question, which is a harder task than answering it and a more useful one when the data cannot.

None of this is a claim to have solved it. It is a statement of what we think the field is short of: not more sensors, and not larger general models, but systems evaluated on whether they know the difference between a finding and an artefact.

Limitations

The following are properties of the method, not defects awaiting a patch. They are listed because a result is only as useful as the reader's ability to discount it appropriately.

• ·Unmeasured confounding cannot be removed from observational records. Randomised protocols address it; passive history does not.
• ·Instrument-mediated confounding, where an intervention changes the signal a device uses to infer the outcome, survives within-person contrast (section 02).
• ·Prior sensitivity on within-person variance is real and documented in the literature this method builds on [4].
• ·Cohort composition bounds transportability. Partial pooling borrows from the people we have, and a person unlike any of them gets little benefit from it.
• ·Adherence is itself a variable. A protocol followed unevenly produces a different estimand from the one specified.
• ·Slow outcomes are out of reach. An intervention whose effect takes a year to appear cannot be settled by a design measured in weeks.

Data handling

Personal health records are processed to answer that person's own questions. Cohort-level parameters are estimated from pooled statistics rather than by exposing one person's record to another. Retention, access, and deletion are set out in the privacy policy.