Describe first. Infer only when the data allow it.

Question

Baseline starts from one idea: a change in someone’s reported experience means more when it is compared with that person’s own history than with an average of other people. Group-level patterns do not transfer reliably to individuals. In one re-analysis of six repeated-measures datasets, person-specific correlations were 2.09 to 4.00 times more dispersed than cross-sectional ones, and 1.63 to 3.43 times after removing temporal dependence [1].

The research question that follows is practical. Given a few weeks or months of one person’s answers, what can be described reliably, what can be inferred, and when must the system refuse? The answer decides what a therapist is shown, and in what words.

What the prototype shows today

The therapist view (Perspective) is a working prototype with fictional patients. It is deliberately descriptive:

• Questionnaires. The Primals Inventory (PI-18) and the Mini-IPIP are each scored on their own range with their original items and scoring. Differences between two assessments are worded only as “increased”, “decreased”, “little change” (under 10% of the scale’s range) or “not comparable”. No trend model, statistical test or composite is computed, and Mini-IPIP differences are not read as personality change.
• Daily check-in. Three experimental questions on 0–10 sliders, each its own series. Summaries per period: answers used, skipped and not comparable, days without a check-in, the observed range, the median day-to-day change, and the latest answer against the previous one.
• Personal history band. The interquartile range of a person’s earlier check-ins, shown only with at least 14 comparable answers spanning at least 14 days. It is not a normal range, threshold, reliable-change index or risk score.
• Rule-based prompts. A few optional prompts, for example when a daily median since the last consultation differs from the earlier median by two points or more. They are labelled unvalidated and link to the answers that triggered them.

The separate personal baseline engine flags a sustained shift against a rolling baseline on synthetic histories. Its settings are working assumptions, not validated values.

What the literature supports

A targeted, single-reviewer review. Each source is labelled by how we read it: full text, preprint (full text of a preprint or accepted manuscript) or abstract only.

• Analytic choices drive single-patient conclusions. Twelve research teams analysed the same patient’s experience-sampling data (122 prompts) and no two chose the same treatment targets [2, full text]. Any analysis we show needs a fixed, versioned recipe.
• Feedback from outcome monitoring has, at best, a small average effect. A Cochrane review of 17 randomised trials (8,787 participants) found a standardised mean difference in symptoms of −0.07 (95% CI −0.16 to 0.01), with low certainty [3, full text]. A broader meta-analysis that includes non-randomised studies reports d = 0.15 [4, abstract]. Baseline cannot claim benefit from its analytics.
• Before-and-after designs have no fixed minimum, but strict requirements. Interrupted time series need an impact model fixed in advance and handling of trend, seasonality, autocorrelation and concurrent events [5, full text].
• Single daily items are plausibly moderate and item-dependent. Within-person reliability of single affect items ranged from about 0.26 (“angry”) to 0.60 (“positive”) in one clinical sample with four prompts a day [6, full text]. We use this only as a range for simulation, not as a property of our items.
• Optimistic evidence is weaker than it looks. An experience-sampling feedback package beat usual care in one trial, but against sampling without feedback the difference was p = 0.053 [7, full text]. Large gains from personalised treatment come from an uncontrolled open trial [8, abstract].
• Negative simulation results are conditional. Poor recovery of person-specific networks and early-warning signals at short series lengths [9, 10, preprints] depends on the generators used. They argue against building discovery tools, not for a universal threshold.

How much data is enough

There is no universal number of observations. How much information a daily series carries depends on its noise and on how strongly each day resembles the last. Two standard results show why (our own application, not a published finding):

For a series with day-to-day autocorrelation \(\varphi\), the mean of \(n\) consecutive days is about as informative as \(n_{\text{eff}}\) independent points. With \(\varphi = 0.5\), 14 daily answers carry roughly as much information about the level as 4 or 5 independent ones.

With within-person reliability \(\rho\), correlations shrink, and an interaction of two items measured with reliability 0.5 each has a reliability of only about 0.25. With several error-prone items the bias can go in either direction [11], so these are intuitions, not corrections.

So sufficiency is a property of the data. Each method must name the quantity whose uncertainty has to fall below a tolerance that is agreed in advance, and refuse otherwise. The prototype’s current count rules stay as necessary conditions, not sufficient ones.

Fig. 1. In one synthetic patient, answers alternate between high and low days while weekly averages stay flat. A median then sits where no answer lies, and one extra check-in can move it by several points. In that fixture, the timestamp of a single check-in decides whether an existing prompt fires. That is why we want distributions shown next to medians, and why the prompt should be relabelled as possibly reflecting day-to-day variation.

Three questions a therapist might ask

First hypothesis (synthetic data only)

H1. On realistic synthetic data where consultations have no effect, but with noisy items, day-to-day dependence, slow drift, fixed-weekday consultations, answers skipped more often on bad days and symptom-triggered scheduling, the prototype’s current “recent versus earlier” prompt (a median difference of at least 2 with at least 3 answers on each side) flags far more consultations than a false-alarm budget declared in advance. A comparison that accounts for earlier trends, is calibrated against comparable non-consultation dates and refuses explicitly keeps false flags within budget, and still detects real effects of a pre-declared size when sessions are planned.

We start here because the prompt already exists, so the answer changes a real decision: keep it, relabel it or retire it. The question can be answered entirely on synthetic data, it is falsifiable against a pre-registered budget, and it tests the refusal behaviour every later feature needs. It does not test whether sessions affect patients, and a favourable result would not validate the prompt clinically. Status: not executed.

Planned evaluation

• A separate generator. Synthetic series are produced outside the app, with day-to-day dependence of 0, 0.3 or 0.6, item reliability of 0.3, 0.5 or 0.7, random or state-dependent missing answers, 4 to 16 weeks of data, and weekly or fortnightly consultations that are either planned or triggered by low answers. At least 1,000 replicates per condition.
• Null and positive conditions. Every method is run where nothing happens and where an effect of pre-declared size and shape exists, including effects mixed with drift, weekday patterns and skipped answers.
• Refusal counts as a miss. A method must keep false alarms within budget, find real effects often enough, and refuse where refusal is required. A method that always refuses cannot pass.
• No peeking. Development, calibration and final evaluation use disjoint seed sets. Everything is frozen and hashed before the final set is generated, which also contains a generator variant not seen during development. The app’s own fictional patients are excluded, because the current thresholds were chosen while looking at them.
• Calibration against comparable dates. The candidate method compares the change around real consultations with the change around non-consultation dates on the same weekday in the same record. This only holds when sessions are planned rather than triggered by symptoms, and it does not correct confounding. Otherwise the method must refuse and fall back to per-consultation rows.
• Different bars for different decisions. Relabelling the current prompt needs no experiment. Retiring it needs evidence that it exceeds the false-alarm budget or is no better than chance. Adopting a replacement needs every criterion met plus independent review, and even then permits only a descriptive or research-mode output. Retiring without a replacement is an acceptable outcome.

All results would be engineering evidence about methods on artificial data, not scientific or clinical validation.

What we will not build

Unless new full-text evidence overturns the review:

• Per-patient network or vector-autoregressive models, and early-warning indicators.
• Open-ended screens such as “show me anything unusual”. The number of comparisons is undefined, so the false-discovery risk is unbounded.
• Population priors, composite scores and reliable-change labels.

If a language model is ever used, it would be local and off by default. It could only draft a structured request that the therapist sees and confirms before anything runs. Explanations would be template-first; a paraphrase would be shown only if every number, date and item in it appears in the computed result. Patient free text would never be sent unless the therapist selects it. No model has been chosen or evaluated.

Approvals before each step

None of these has been completed. Real-data work, such as a reliability and missing-data study of the daily items, comes only after G2 and G3.

Limitations and open questions

• The review. Targeted, single-reviewer search. Two decision-relevant sources were read as abstracts only and two as preprints.
• Our items. Reliability and sensitivity to change of the three daily questions are unknown. They may need to be replaced by validated short measures or by items the patient chooses.
• Tolerances. Which interval width, false-alarm budget and minimum meaningful difference are acceptable for a therapist-facing statement is a joint clinical and scientific decision that has not been made.
• Missing answers. How skipping relates to how someone feels in real use, and whether reminders change it, is unknown.
• Scheduling. Without knowing whether consultations were planned or booked because of symptoms, before-and-after differences cannot be separated from regression to the mean.
• Benefit. Whether any descriptive view changes therapist decisions, and whether that helps patients, is untested. The outcome-monitoring evidence suggests small effects at best.

Earlier design notes

Earlier versions of this page described a proposed Personal Affect Model: a neural state-space model over conversation embeddings, Bayesian change-point detection, a retrieval memory and a ranking of support options. It was never built or trained. We have withdrawn it. The review above found no support for per-patient dynamic models or early warnings at the history lengths we expect, and support matching is not part of current work.

References

External research. None of these papers is Baseline work, and none is evidence that Baseline works.

1. Lack of group-to-individual generalizability is a threat to human subjects research. Fisher, Medaglia & Jeronimus, PNAS, 2018. doi:10.1073/pnas.1711978115
2. Time to get personal? The impact of researchers’ choices on the selection of treatment targets using the experience sampling methodology. Bastiaansen et al., Journal of Psychosomatic Research, 2020. doi:10.1016/j.jpsychores.2020.110211
3. Routine use of patient reported outcome measures (PROMs) for improving treatment of common mental health disorders in adults. Kendrick et al., Cochrane Database of Systematic Reviews, 2016. doi:10.1002/14651858.CD011119.pub2
4. Using progress feedback to improve outcomes and reduce drop-out, treatment duration, and deterioration: A multilevel meta-analysis. de Jong et al., Clinical Psychology Review, 2021. doi:10.1016/j.cpr.2021.102002
5. Interrupted time series regression for the evaluation of public health interventions: a tutorial. Lopez Bernal, Cummins & Gasparrini, International Journal of Epidemiology, 2016. doi:10.1093/ije/dyw098
6. Examining the concurrent and predictive validity of single items in ecological momentary assessments. Song, Howe, Oltmanns & Fisher, Assessment, 2023. doi:10.1177/10731911221113563
7. A therapeutic application of the experience sampling method in the treatment of depression: a randomized controlled trial. Kramer et al., World Psychiatry, 2014. doi:10.1002/wps.20090
8. Open trial of a personalized modular treatment for mood and anxiety. Fisher et al., Behaviour Research and Therapy, 2019. doi:10.1016/j.brat.2019.01.010
9. Investigating the feasibility of idiographic network models. Mansueto et al., Psychological Methods, 2023. doi:10.1037/met0000466
10. Anticipating critical transitions in psychological systems using early warning signals: Theoretical and practical considerations. Dablander et al., Psychological Methods, 2023. doi:10.1037/met0000450
11. Measurement error and person-specific reliability in multilevel autoregressive modeling. Schuurman & Hamaker, Psychological Methods, 2019. doi:10.1037/met0000188