Applications in Clinical Psychology and Mental Health

33.1 Clinical Longitudinal Research: The Terrain

Clinical questions about change fall into a handful of families, and each family routes to a part of this book. Whether a treatment works, and how fast, is a question about symptom trajectories, answered by the growth models of Chapters 13, 14, and 19. For whom it works is a question about heterogeneity, approached with the guarded mixture models of Chapter 22 and the tree methods of Chapter 31. Who relapses, and when, is a timing question, answered by the survival models of Chapter 29. How symptoms interact within a patient is a dynamics question, answered by the multilevel vector-autoregression and network methods of Chapters 25 and 28. Whether an impending deterioration can be seen coming is a monitoring question, approached with the state-space and nonlinear methods of Chapters 26 and 32, with all their cautions. And how to deliver an intervention at the right moment is an optimization question, answered by the micro-randomized designs this chapter introduces. Figure 33.1 draws the routing, and Table 33.1 sets it out with the estimands and exemplar literatures.

Note. Each family of clinical question routes to the part of the book that answers it. The routing is estimand-first: the question determines the method, not the reverse. A single study usually asks several of these questions, and the integration of the corresponding analyses, in a principled sequence with honest reconciliation, is the subject of this chapter’s case studies.

Three realities of clinical longitudinal data shape every analysis that follows. Symptom scales may not measure the same construct the same way as treatment proceeds, a response shift that the invariance methods of Chapter 18 can test and that undermines a naive comparison of scores across time if ignored. Frequent assessment of symptomatic patients carries burden and reactivity, so the measurement schedule is an ethical and estimand question, not merely a logistical one. And patients are nested in therapists and sites, a multilevel structure that inflates false-positive rates if unmodeled. To these the trials tradition adds a discipline psychology is still absorbing: the estimand framework of the ICH E9(R1) addendum, which insists that the handling of dropout and rescue medication be specified as part of the estimand itself, so that a treatment-policy strategy (the effect regardless of adherence), a hypothetical strategy (the effect had all patients adhered), and a while-on-treatment strategy answer genuinely different questions and must not be conflated. Table 33.2 translates these strategies for the psychologist, and Case Study A puts them to work.

33.2 Case Study A: The Trial, Taken Seriously

The therapy_rct data are a randomized trial of two hundred forty patients, half assigned to an active treatment and half to control, with the Hamilton depression rating scale measured weekly for twelve weeks. The analysis proceeds in a deliberate sequence, each step motivated by the last, and Table 33.3 is the decision log that records the reasoning, the reproducible-reasoning exhibit that a finished paper omits. Description and visualization come first, per the book’s standing rule. The primary analysis is a growth model of the symptom trajectory with a random intercept and slope, and its estimand is the difference between arms in the rate of change. The treatment arm improves faster, by half a Hamilton point per week more than control (\(-0.51\) points per week for the arm-by-time interaction), so that by week twelve the model-implied severity is \(8.5\) in the treatment arm against \(14.6\) in control, a difference that crosses the threshold from moderate to mild depression. A secondary generalized-linear mixed model translates the continuous trajectory into the outcome a clinician acts on, remission, defined as a Hamilton score below seven, and finds the odds of remission at week twelve many times higher under treatment. Figure 33.2 shows the trajectories and, beneath them, the fact that threatens the whole conclusion.

Note. Panel (a): the fitted growth model (lines) and observed weekly means (points) for the therapy_rct trial. The treatment arm improves faster (arm-by-week slope \(-0.51\)), reaching a model-implied Hamilton score of \(8.5\) at week twelve against \(14.6\) in control. Panel (b): retention falls to about fifty-five percent by week twelve, and the dropout is symptom-dependent, patients with higher current symptoms are likelier to leave. Attrition of this magnitude and this mechanism can bias the primary estimate, which is why the sensitivity analysis is not optional.

That fact is attrition. Forty-four percent of patients did not complete the trial, and a discrete-time hazard model of dropping out shows the dropout to be symptom-dependent: patients with higher current symptoms are more likely to leave (\(p < .001\)). The primary growth model, fit by full-information maximum likelihood, is valid if the dropout is missing at random given the observed trajectory, which the symptom-dependence makes plausible but not certain, because the value that triggers dropout is the one that goes unobserved. This is the missing-not-at-random worry of Chapter 6, and the clinical-evidence obligation is to probe it, not to assert it away. Two sensitivity analyses do so, and Figure 33.3 displays them. A tipping-point analysis imputes each dropout’s missing scores from the model and then penalizes the treatment-arm dropouts by adding a fixed number of Hamilton points, on the hypothesis that treated patients who leave fare worse than the model predicts; sweeping that penalty from zero to eight points, the treatment benefit attenuates but remains significant throughout, so it would take an implausibly large and arm-specific departure from missing-at-random to overturn the conclusion. A shared-parameter joint model, which fits the trajectory and the dropout process together with a shared random slope, reaches the same estimate as the naive model (\(-0.512\) against \(-0.514\)) and finds the dropout only weakly associated with the slope, corroborating the missing-at-random assumption directly. The two sensitivity analyses converge, and that convergence, not the primary estimate alone, is the robust finding.

Note. Panel (a): a tipping-point analysis penalizes treatment-arm dropouts by a fixed number of Hamilton points (the horizontal axis) and refits; the arm-by-week benefit attenuates but stays significant even under an eight-point penalty, so overturning it requires an implausible missing-not-at-random departure. Panel (b): a shared-parameter joint model of trajectory and dropout reaches essentially the naive estimate (\(-0.512\) versus \(-0.514\)) with a near-zero dropout association, corroborating missing-at-random. The convergence of the two analyses is the robust conclusion.

A final, honestly labeled step asks whether the average effect hides responder heterogeneity. An exploratory growth mixture identifies two latent trajectory classes, a fast-responding group and a slow-responding one, but the analysis is reported with every guardrail of Chapter 22: the classes are described as an exploratory hypothesis, their number is not treated as discovered, and they are not reified into clinical subtypes on the strength of a single sample. The teaching payload of the whole case is the sequencing, description before modeling, primary before secondary, and sensitivity as obligation, and the translation of a trajectory difference into the remission language a clinical audience needs.

33.3 Case Study B: Symptom Dynamics and Personalized Structure

The affect_ema data follow a sample through many days of ecological momentary assessment, and the clinical interest is in the dynamics: how a patient’s stress spills over into negative affect, how affect carries forward, and how these dynamics differ across patients. The analysis begins with measurement and description, because momentary items are noisier than questionnaire scales: a multilevel reliability analysis shows that thirty-six percent of the variance in momentary negative affect lies between persons, and the dynamic indices of Chapter 7, a mean autocorrelation of \(0.37\) and a mean successive difference of \(0.60\), describe the tempo and instability of the series before any model is imposed. The primary dynamic analysis is a multilevel vector-autoregression, which estimates each variable’s dependence on the recent past of itself and the others, with random effects that let the dynamics differ by person. It finds a clear stress-to-affect spillover, a lagged effect of stress on negative affect of \(0.24\), and an affective inertia, a carry-forward of negative affect, of \(0.31\), both varying across patients.

The discipline the case study exists to teach is that these dynamics can be represented three ways, and the three are one truth seen through different lenses, to be reconciled rather than reported selectively. The multilevel model states the effects as regression coefficients with random variation. The same lagged coefficients, arranged as a matrix, are a temporal network whose directed edges are exactly those coefficients, the representation of Chapter 28. And the random effects are the raw material for idiographic portraits of individual patients. Figure 33.4 shows the first two lenses together, the temporal network of fixed effects and the distribution of person-specific spillovers, and Table 33.4 reconciles what each lens claims. The network figure must carry the claims-ladder discipline of Chapter 28: its edges are conditional associations, not proven mechanisms, and a centrality claim requires the stability analysis that chapter mandated. The reconciliation is the point. A paper that presented the network as a new finding beside the multilevel model, as though they were separate results, would be double-counting one analysis; a paper that presented only the network, with its vivid picture, would be hiding the uncertainty the coefficients carry.

Note. Panel (a): the temporal network of the affect_ema dynamics as the lagged fixed-effect matrix of a multilevel vector-autoregression; a directed edge is a lagged coefficient, a conditional association and not a proven mechanism. Panel (b): the person-specific stress-to-affect spillover varies across patients around its mean of \(0.24\), the random dynamics that a single average would hide. The network and the multilevel model are one analysis in two representations, to be reconciled, not reported as separate findings.

Idiographic analysis then asks what can be said about an individual patient, and here the pooling lesson of Chapter 25 returns with clinical stakes. Figure 33.5 contrasts, for two patients, the person-specific estimate computed from that patient’s data alone with the shrunken estimate the multilevel model assigns. For a patient with ample, consistent data the two agree closely; for a patient with noisier data they diverge substantially, the multilevel model pulling the unstable individual estimate toward the group. Reporting the person-specific number alone would over-trust a noisy estimate; reporting the shrunken number alone would understate genuine individuality. The clinical translation must be correspondingly careful: a person-specific dynamic is a hypothesis about that patient to be checked against their history and their clinician’s knowledge, not a validated individual fact, and the ethics of reporting it, the patient’s privacy, the temptation to over-interpret a single striking coefficient, are part of the analysis, not an afterthought.

Note. For two patients, the stress-to-affect spillover estimated from that patient’s data alone (person-specific) and the estimate the multilevel model assigns after borrowing strength across patients (shrunken). For a patient with consistent data the two nearly coincide; for a patient with noisier data they diverge, the multilevel model regularizing the unstable individual estimate. The person-specific number over-trusts thin data; the shrunken number regularizes it. Neither is the whole story, and a clinical claim about an individual must acknowledge both.

33.4 Case Study C: Monitoring, Prediction, and Just-in-Time Intervention

Digital mental health delivers assessment and intervention through a phone, and it routinely conflates three activities that are logically distinct: optimizing an intervention, predicting risk, and monitoring for transitions. The case study separates them, because each is a different estimand with a different design and standard of evidence, as Table 33.5 sets out. The just-in-time adaptive intervention, in the framework of Nahum-Shani et al. (2018), delivers support at decision points, tailored to the person’s momentary state, to affect a proximal outcome, and Figure 33.6 draws its architecture. The question it poses, does delivering the prompt now improve the proximal outcome, and for whom, is an intervention-optimization estimand, and the design that answers it is the micro-randomized trial, in which the intervention is randomized at each decision point so that its momentary causal effect is identified (Klasnja et al., 2015).

Note. At each decision point, a tailoring variable (the momentary state) informs whether an intervention is delivered, and the intervention affects a proximal outcome, feeding back into the next decision point. In a micro-randomized trial the intervention is randomized at each available decision point, which identifies the causal excursion effect, the momentary effect of delivering the prompt, averaged over the randomization distribution, and its moderation by the tailoring variable.

The mrt_ema data are a micro-randomized extension in which a brief coping prompt is randomized at each available decision point and the proximal outcome is the negative affect shortly after. The causal excursion effect is estimated by a weighted-and-centered regression that is robust to misspecification of the control model (Boruvka et al., 2018), and it recovers the planted effect: the prompt reduces proximal negative affect by about half a point when first delivered, its benefit wanes across the study as the person habituates, and it works more strongly when the person is stressed. Figure 33.7 shows the excursion effect over time, and the waning is itself the clinically actionable finding, because an intervention whose effect decays should be varied or spaced rather than repeated identically. This is optimization, not prediction: the estimand is the effect of an action, and the evidence is a randomized contrast.

Note. The estimated causal excursion effect of the coping prompt on proximal negative affect in the mrt_ema micro-randomized trial, over study day, with the planted truth dashed. The prompt’s proximal benefit is largest when first delivered (about \(-0.46\)) and wanes across the study as the person habituates. The waning is the actionable result: an intervention whose momentary effect decays should be spaced or varied, a design conclusion only a micro-randomized trial can support.

Prediction is a different activity with a different estimand, the probability of a future state, and the discipline of Chapter 31 governs it. A risk-flag model forecasting momentary negative affect, evaluated by person-grouped cross-validation and measured against the persistence baseline, beats that baseline by a real but bounded margin (a cross-validated coefficient of determination of \(0.49\) against the baseline’s \(0.26\)), and its calibration must be checked, not merely its discrimination, as Figure 33.8 shows. Monitoring is a third activity, the detection of an approaching transition, and the early-warning verdict of Chapter 32 applies unchanged: a rising indicator in one patient’s stream is a monitoring hypothesis, not a validated alarm, and the base-rate and analyst-degrees-of-freedom cautions bind here as they did there. The teaching payload is the separation itself, because a digital-mental-health study that reports a predictive model as though it optimized an intervention, or an early-warning signal as though it predicted risk, has conflated three questions that require three designs.

Note. Panel (a): the calibration of a person-grouped cross-validated model forecasting momentary negative affect, binned predicted against observed; points near the diagonal indicate good calibration. Panel (b): the model’s cross-validated coefficient of determination (\(0.49\)) against the persistence baseline (\(0.26\)), the honest margin. Prediction is judged by out-of-sample skill over a baseline and by calibration, not by in-sample fit, and it is a different activity from the intervention optimization of Figure 33.7.

33.5 Domain Synthesis

The three case studies share a spine, and naming it is the chapter’s synthesis. Each visualized before it modeled, named its estimand before it chose a method, and analyzed its sensitivity as a matter of course rather than on demand. Each also enforced a claims discipline particular to its methods: the trial bounded its conclusion with missing-data sensitivity, the dynamics study reconciled its representations rather than multiplying them, and the digital-health study separated optimization from prediction from monitoring. Figure 33.9 draws the clinical claims ladder that fixes the language a longitudinal result has earned to the evidence supporting it, and Table 33.6 is the reporting checklist a clinical journal should expect. The common reviewer objections to clinical longitudinal work, that the average effect is taken to settle what a treatment does for an individual, that more frequent measurement is assumed to be more clinical truth, that a network figure is read as a mechanism, that a forecast is oversold, are each answered by a discipline the case studies modeled. The domain literatures each add their own texture, the depression and anxiety ecological-momentary-assessment tradition (aan het Rot et al., 2012; Hamaker & Wichers, 2017), the experience-sampling study of psychosis (Myin-Germeys et al., 2009, 2018), the instability literature in borderline personality disorder (Trull et al., 2008; Ebner-Priemer & Trull, 2009), the idiographic-network exemplars (Fisher et al., 2017; Epskamp et al., 2018), but the analytic spine is common, and it is the spine this book has built toward.

Note. The language a clinical longitudinal result has earned is fixed to the evidence that supports it. Description and association are available from most designs; a robust or causal-in-design claim requires randomization or a sensitivity analysis that bounds the missing-data threat; an individual-level or mechanistic claim requires idiographic validation or an experimental manipulation. Writing at the rung the evidence reaches, and no higher, is the discipline the three case studies share.