Separating Reporting Artifacts from Mood Dynamics by Timescale

Daily mood diaries are the main measurement tool of digital mental health, and they are known to be distorted. People copy yesterday's answer. They avoid the ends of the scale. They skip entries on their worst days. Analysts usually see only the final diary series and cannot tell which of its structure comes from the person's mood and which comes from the way the person fills in the form. This proposal argues that these two sources can be partly pulled apart because they act on different timescales and on fluctuations of different sizes.

The measurement tool is detrended fluctuation analysis (DFA), which removes local trends and then asks how the spread of a series grows as the observation window lengthens. A multifractal extension, MF-DFA, asks the same question separately for large and small fluctuations. The claim is that answer-copying (anchoring) inflates persistence only at short windows and leaves a visible bend in the scaling curve. Scale compression and symptom-dependent skipping instead damage the large-fluctuation end of the multifractal profile. A scale-resolved reading of the diary can therefore flag and partly correct reporting distortion without an external ground truth. The passive wearable streams collected alongside the diaries serve as an unbiased witness at long timescales.

Core Claim

The obvious combination of these fields would compute a Hurst exponent (the single number DFA returns; 0.5 means no memory, above 0.5 means persistent memory) for mood diaries and for wearables, then read their difference as "bias." This is the file's Gap 2. That design is weak, because mood and step counts are different constructs, and a difference in their exponents says nothing about who is misreporting.

The sharper claim concerns the reporting process itself. Treat a diary entry as the output of a known family of distortions applied to a latent mood trajectory. Each distortion then has a characteristic footprint on the fluctuation function $F(n)$ (how much the detrended series spreads within windows of $n$ days) and on the generalized exponents $h(q)$ (the scaling slope when fluctuations are weighted by their size through order $q$). The footprints are specific enough to separate distortions from each other and from genuine long memory in mood.

The central example is anchoring, which works like a short autoregressive smear. If a respondent reports roughly $r_t = c\,r_{t-1} + (1-c)\,g(m_t)$, where $r_t$ is the day-$t$ report, $m_t$ the latent mood, $g$ the mapping onto the scale, and $c$ the carryover weight, then at windows shorter than a few multiples of $-1/\ln c$ days the DFA slope is pushed upward. Beyond that crossover, the slope returns to that of $m_t$.

A single lag-1 autocorrelation cannot make this distinction, because it lumps the smear together with true persistence. The scaling curve can, because the two produce different shapes. The claim is testable in simulation, where the latent mood is known, and in real cohorts, where wearables give an independent check.

Relation to Prior Work

Prior work supplies the method but has never pointed it at the reporting process. Multiscale Fractal Analysis on EEG Signals for Music-Induced Emotion Recognition uses MF-DFA features of 60-second EEG to predict 9-point valence and arousal ratings. It treats those ratings as clean labels, whereas we treat the ratings themselves as the signal under study.

The same paper also constrains our design. It warns that preprocessing can truncate the singularity spectrum, and this is why we analyze raw ordinal diaries with only explicit dequantization. Fractional dynamics foster deep learning of COPD stage prediction motivates the direction: it replaces an effort-dependent human measurement (spirometry) with multifractal features of passive physiology. It keeps no human report in the loop, while we keep the report and characterize its distortion.

Detrended Partial Cross Correlation for Brain Connectivity Analysis supplies the cross-series tool. It decomposes correlation between fMRI series by timescale while removing confounders, and it shows scale-specific links that Pearson correlation misses. We move that tool from millisecond neuroimaging to daily mood-versus-wearable coupling.

A Tale of Two Structures serves as a conceptual precedent. It shows that the generating process of a sequence leaves a Hurst signature: human text sits near $H \approx 0.65$, and instruction tuning shifts it. We apply the same logic to the human act of reporting.

Digital-health studies motivate the gap. Assessing Real-Time Moderation for Developing Adaptive Mobile Health Interventions for Medical Interns names self-report bias and missingness as limitations but has no tool to separate them from mood change. Personalised depression forecasting using mobile sensor data and ecological momentary assessment handles individual reporting style only through per-subject standardization, which removes level and spread but not temporal distortion.

A final constraint comes from Gap 4 of the file. Somatic work reads a narrow spectrum as disease ("health is complex"), while financial and EEG work reads a wide spectrum as distress. We therefore make no assumption about what spectrum width means clinically. We use width only as a diagnostic of the reporting channel.

Research Program

The first component is a forward model of reporting. Latent mood trajectories are simulated with controlled persistence, from $H$ of 0.5 to 0.9, and controlled multifractality, through multiplicative cascades. These trajectories are then passed through composable distortions:

  • quantization to the 1–10 or 1–9 scales actually used;
  • anchoring with carryover $c$;
  • end-aversion or desirability compression that squeezes extremes;
  • missingness whose probability rises with the latent severity;
  • slow drift from fatigue.

For every combination we estimate $F(n)$ and $h(q)$ at the realistic series lengths of roughly 70 days (StudentLife) and 180 days (the Intern Health Study). The output is an identifiability map showing which distortions produce distinguishable footprints at these lengths and which do not.

MF-DFA on 180 points is fragile. Negative $q$ also diverges on zero-variance windows, which straight-line answering creates on purpose. For both reasons we restrict $q$ to roughly $[-3, 3]$ and dequantize ordinal ties with uniform jitter. We report the fraction of degenerate windows as a separate artifact score rather than hiding it.

The second component is an estimator. It fits the forward model to each person's diary by simulation-based inference. The summary statistics are the full scale-resolved $F(n)$ curve, $h(q)$, and the crossover location. The estimator returns posterior estimates of carryover, compression, and severity-linked missingness, together with the latent long-window exponent.

The third component is empirical validation, using wearables as the unbiased witness. Step counts and sleep are not subject to anchoring or desirability. Detrended cross-correlation between mood and wearables at long windows should therefore reflect real coupling. At short windows, the same cross-correlation should be diluted in proportion to the person's estimated carryover.

Baselines

The naive reference point is standard single-slope DFA on the raw diary, taking reports at face value. This is what Gap 1 would do. Beating it means recovering the latent exponent in simulation with lower error whenever anchoring or missingness is present, while matching it when no distortion is present.

The strongest simple competitor for detecting distortion is the set of careless-responding and dynamics indices clinicians already compute: lag-1 autocorrelation, the long-string rate of identical consecutive answers, and within-person standard deviation. These indices target exactly the anchoring and compression effects we model, so they are the real test. They receive the same series, and a regularized regression over them receives the same cross-validation budget as our estimator.

Beating them requires one of two outcomes. The first is a significantly more accurate estimate of carryover and of the latent exponent in simulated cases where true persistence and carryover coexist, since this is where lag-1 autocorrelation should confound them. The second is incremental predictive value on real data after these indices are already included.

The strongest model-based competitor is a state-space model: AR(1) latent mood plus ordinal measurement noise plus an explicit carryover term, fit by maximum likelihood. It gets the same data and a matched number of free parameters. It wins if the latent process is truly short-memory, and our method should win if the latent mood has long memory. The simulation grid covers both regimes, so the outcome is determined rather than argued.

For downstream forecasting, the strongest reported numbers come from Personalised depression forecasting using mobile sensor data and ecological momentary assessment on the MAIKI dataset:

  • same-day PHQ-2 MAE of 0.801 with subject-dependent standardization, against 1.062 non-personalized;
  • one-day-ahead PHQ-2 MAE of 1.349 with transfer learning, against 1.539 at baseline.

We will rerun their standardization and transfer pipelines on identical splits, then add our artifact-corrected features. Beating 1.349 one-day-ahead under the same splits is the bar. Access to MAIKI is not guaranteed. If access fails, the forecasting comparison moves to StudentLife, where the file reports a depression-score RMSE of 3.5 ± 3.1 for a spatiotemporal graph network in Monitoring Behavioral Changes Using Spatiotemporal Graphs. That error is so wide relative to its mean that we treat it as a weak reference only.

The key ablation strips the estimator down in stages. First we remove the crossover (a single DFA slope). Second we remove $q$-dependence (monofractal only). Third we remove the degenerate-window score. Each step shows whether scale resolution, size resolution, or straight-lining detection carries the gain.

Why not just…?

Why not just use lag-1 autocorrelation and long-string counts to catch anchoring? This is the most serious alternative. For pure copying with no real mood persistence, these counts may be sufficient, and the simulation will show that honestly. Their limitation is conceptual: lag-1 autocorrelation is high both when a person copies answers and when their mood truly has memory. The DFA curve separates the two because copying bends it only below the crossover. The decisive simulation cell combines true long memory with carryover. If the simple indices estimate carryover as well as our estimator there, we drop the fractal machinery for anchoring and keep it only for missingness and compression.

Why not just fit a state-space model with a measurement-error layer? This is the principled psychometric answer. It will win if mood is short-memory, which is an empirical question no paper in the file has settled for self-reports. Its standard forms assume exponentially decaying memory. Fractional dynamics foster deep learning of COPD stage prediction reports that sequence models without scaling structure fall well short on long physiological series: 78.5% for an LSTM against 98.66% for fractional features. That is a different domain and is suggestive only. The head-to-head comparison on the simulation grid, and on real diaries through the wearable-coupling test, settles the matter directly.

Why not just standardize per person and move on? Per-subject standardization gave the 25% same-day gain reported on MAIKI. It is simple and should always be applied first; we apply it inside our pipeline too. It removes each person's typical level and spread. It cannot remove a temporal smear or skipped bad days, because those change the order and spacing of reports, not just their scale. The forecasting comparison tests whether the temporal correction adds anything beyond standardization. The paper's own one-day-ahead result, where standardization was not enough and transfer learning was needed, suggests there is room.

Proposed Experiments and Decisive Checks

The first check is the simulation identifiability map. It gives recovery error for carryover, compression, missingness strength, and latent $H$ at 70 and 180 days, against every baseline above. If footprints are not separable at 180 days, the proposal is falsified at that length, and we report the minimum length at which they become separable.

The second check uses the Intern Health Study, with daily mood and Fitbit data for 1,565 interns over six months, as described by NeCamp et al.. We predict that interns with high estimated carryover show weaker mood–steps and mood–sleep detrended partial cross-correlation at short windows but not at long ones, controlling for day-of-week and randomized notification. If short- and long-window coupling fall together, the anchoring interpretation is wrong.

The third check reuses the same cohort's micro-randomization. That study found that mood tips sent to high-mood interns lowered reported mood. We test whether this reactivity concentrates in participants whom our estimator flags for compression or carryover, which would indicate a reporting rather than an affective response. No reported result was found on Lacuna for fractal analysis of this cohort.

The fourth check is the MAIKI forecasting comparison against the 1.349 one-day-ahead MAE, with StudentLife as a fallback.