Evidence Review: CBT-I for Insomnia with Co-occurring Depression or Anxiety

Reviewed by Dr. Margarita Krasnova, MD · Last reviewed 2025-12-12

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Treating Insomnia When Depression or Anxiety Is Also Present: A Scoping Review of Available Evidence on CBT-I

Abstract

Objective: To examine whether cognitive behavioral therapy for insomnia (CBT-I), compared with usual care or an inactive insomnia control, improves depressive or anxiety symptoms in adults with insomnia and a co-occurring disorder or clinically significant symptoms.

Methods: Forty-one retained full-text reports were assessed against the review question and linked to their parent studies. Evidence from diagnosed or clinically significant comorbidity was distinguished from studies admitting mild symptoms and from combined depression/insomnia treatment packages. Outcomes were reconciled by scale, comparison, assessment time and analysis population. Synthesis was structured by treatment comparison without statistical pooling. Result-specific RoB 2 worksheets and GRADE certainty profiles were completed by a first assessor; independent verification has not been performed.

Results: Eleven reports contributed direct comparative results for the core population, including a baseline-defined subgroup reported within a broader trial; three supplied linked companion information. Five additional reports informed broader-population or combined-treatment comparisons, and 22 were retained as context or excluded from the target comparison. Three reports of adjusted PHQ-9 differences favored CBT-I at 8–12 weeks: −3.34 points (95% CI −4.70 to −1.98), −3.91 (−5.20 to −2.62), and −3.03 (−3.56 to −2.50); the last combined qualifying subgroups from two parent trials. Other studies evaluated different scales and treatment contrasts. Benefits on depression were less consistent when CBT-I was added to active depression treatment. Differential attrition, self-reported outcomes, selected-subgroup analyses and source-reporting inconsistencies limited confidence. Anxiety evidence was less developed than depression evidence. Treatment-related intolerance of sleep restriction was reported in one small trial.

Conclusions: Within the accepted evidence pool, low-certainty evidence supports depressive symptom-score improvement with CBT-I, but does not establish uniform improvement in depression remission or superiority of one delivery format. Anxiety-disorder-specific effects and the magnitude of incremental benefit alongside active depression treatment remain uncertain. Interpretation should preserve each study's actual comparator, outcome and follow-up conditions.

Keywords: insomnia; cognitive behavioral therapy for insomnia; CBT-I; depression; anxiety; sleep; scoping review; evidence review

Introduction

Insomnia and depression can coexist and create overlapping treatment needs. Treating depression does not necessarily resolve insomnia, and improving sleep may have consequences for mood beyond the sleep items included in common depression scales. Trials have therefore evaluated insomnia-focused treatment both as an addition to depression treatment and as an intervention compared with waiting, education or usual care. These designs answer related but different clinical questions. [1–9]

The distinction is important when interpreting benefit. Improvement within a CBT-I group may reflect treatment, concurrent care, natural fluctuation or regression toward the mean. The relevant comparative estimate is the difference from a suitable control. Likewise, superiority over a waiting group does not establish superiority over another active psychotherapy, and an association between improved sleep and improved depression does not by itself establish a causal mediating mechanism.

This review focuses on adults with insomnia and qualifying depression or anxiety. It separates those populations from insomnia samples in which mood symptoms were measured but were not required at entry, and from prevention cohorts without qualifying baseline comorbidity. It also distinguishes primary trial reports from analyses of overlapping participants. Its contribution is an explicit comparison of symptom severity, remission, durability and treatment burden while preserving these clinical and analytical distinctions.

Methods

Evidence pool and eligibility

This is a physician-authored scoping review of available evidence, not a claim of a comprehensive PRISMA-compliant systematic review or meta-analysis. The purpose is to organize the available literature around a focused clinical question, identify which studies answer it most directly, distinguish direct evidence from adjacent literature, and make uncertainty explicit.

The review used an available full-text evidence pool assembled through structured literature retrieval and subsequent source-level review. The evidence pool was finalized and reviewed on 2025-12-12. Forty-one retained full-text reports formed the principal reviewed pool. A later broad retrieval was also used as an evidence-mapping resource; it identified additional recent and adjacent reports, including protocols, uncontrolled studies, secondary analyses, implementation studies, and broader insomnia populations. Those records were not automatically treated as direct evidence merely because they were relevant to insomnia, depression, or anxiety.

Because historical search and retrieval completeness cannot be established to the standard required for a conventional systematic review, the report counts in this manuscript describe the reviewed evidence pool rather than the entire world literature. The review therefore emphasizes directness and clinical interpretability rather than a claim of exhaustive coverage.

The core population comprised adults aged at least 18 years with insomnia disorder or clinically significant insomnia symptoms and a diagnosed depressive/anxiety disorder or an explicitly qualifying clinical-symptom subgroup. Diagnostic confirmation and study-defined clinical thresholds were recorded. For example, PHQ-9 ≥10 subgroups were distinguished from whole samples admitted with PHQ-9 >4. A mean baseline score alone was not taken as proof that all participants met the criterion.

CBT-I included multicomponent cognitive and behavioral sleep treatment delivered individually, in groups, digitally or with guidance. Comparators included usual care, waitlist, sleep hygiene, attention control or placebo insomnia interventions. Comparisons that held depression treatment common to both arms were distinguished from those in which depression treatment also differed. Uncontrolled pre/post studies and active-treatment sequences without a concurrent inactive comparator did not contribute to the main treatment-effect synthesis.

Mild-or-greater symptom studies were analysed in a separate extension, apart from the clinical-severity population. Integrated CBT for depression and insomnia versus usual care was also considered separately, because the resulting effect cannot be attributed specifically to CBT-I. This distinction was clarified during the present review and is not represented as a prospectively registered analytical decision.

Report linkage, extraction and synthesis

Reports were linked by trial identity, participants, interventions and source descriptions. The Henry report combines qualifying participants from DIALS and OASIS; its estimates were not counted again as independent parent-trial effects. The TRIAD trajectory and sleep-duration reports were treated as companions. The two different Blom trial families and the unrelated studies sharing the acronym EPIC were kept distinct. [5,9,12–14]

Outcome extraction recorded the measure, time point, contrast, analysis model, statistic, uncertainty interval and relevant denominator. Randomized, treatment-starting, observed and analyzed populations were distinguished. Adjusted mean differences, interaction coefficients, observed standardized effects and within-group changes were not interchanged. Source discrepancies were carried forward as explicit qualifications. A matching interval was not invented when only a test or effect magnitude could be supported.

The synthesis emphasized depression and anxiety symptom severity and remission. Insomnia outcomes, well-being, discontinuation and reported harms provided additional clinical context. End-of-treatment comparisons were distinguished from later follow-up and from assessments after control crossover. Findings were grouped by the clinical comparison, with delivery mode treated descriptively rather than as an explanation of treatment differences.

No pooled effect was calculated. The reported data include different scales, adjusted endpoint differences, longitudinal interactions, combined-parent subgroup analyses and incompletely documented variances. A common PHQ-9 display shows selected directly reported estimates without weights or a summary diamond. Studies with tests alone remain in the narrative and evidence table so that availability of a convenient effect estimate does not determine inclusion. The reporting approach draws on the structure of synthesis without meta-analysis described in SWiM. [20]

Appraisal and confidence

A source-based critical assessment considered randomization and allocation, deviations from assigned treatment, missing outcomes, outcome measurement, selective reporting, precision, applicability, and the possibility of overlapping participant samples. Where information was unknown, it was recorded as unknown. Companion and subgroup analyses were not automatically assigned the evidentiary weight of their parent trials, and reports with unclear assignment mechanisms were interpreted more cautiously.

Terms such as low certainty in this manuscript are used as transparent summaries of these limitations rather than as a claim that this public evidence review underwent a fully independent, journal-grade GRADE adjudication. The practical question is how much confidence a clinician should place in a particular finding after considering study design, directness, precision, attrition, measurement, and consistency.

Results

Disposition and study characteristics

Within the principal 41-report pool, eleven reports provided direct comparative findings relevant to the core population, three supplied companion information, five provided broader-population or combined-treatment evidence, and 22 served as context or did not meet the target comparison. The categories are report-level: the GoodNight primary report provides both a qualifying-subgroup finding and broader whole-cohort results, and Henry combines two parent trials. Consequently, report counts are not independent-study or participant counts. No total participant number was obtained by adding overlapping or differently defined analysis populations.

The later broad retrieval reinforced why this hierarchy is necessary: many apparently relevant recent papers involved insomnia populations without qualifying depression/anxiety at entry, uncontrolled pre/post designs, protocols without outcomes, implementation/process studies, or secondary analyses. These reports are useful for mapping the field but should not inflate the apparent amount of direct evidence for the central clinical question.

Table 1. Main comparative evidence and denominator distinctions

Depressive symptoms relative to inactive insomnia controls

Schuffelen reported adjusted PHQ-9 differences of −3.34 points at 12 weeks (95% CI −4.70 to −1.98) and −2.83 at 24 weeks (−4.23 to −1.43). Both groups could continue usual care; the control group received digital treatment after the 24-week assessment. EPIC reported a −3.91-point difference at 10 weeks (−5.20 to −2.62). Depression was a secondary outcome in EPIC, whose co-primary outcomes concerned recognition of emotional facial expressions. [7,8]

Henry's combined DIALS/OASIS subgroup analysis reported differences of −3.03 PHQ-9 points at 8–10 weeks (−3.56 to −2.50) and −2.74 at 22–24 weeks (−3.34 to −2.15). Removing the PHQ-9 sleep item did not alter the reported benefit. These results support improvement in depressive symptoms beyond merely counting a better sleep-item response, but the combined subgroup report does not supply all information needed for a separate complete appraisal of each parent trial. [9]

Table 3. Directly reported adjusted effects at the first post-treatment assessment, without pooling. The three rows represent four parent trials because Henry combines DIALS and OASIS. They are displayed for scale-specific interpretation, not as a new meta-analysis or a comparison of delivery formats. Later results from the same reports are not added as independent observations.

Chan provides a separate CES-D result. Its week-6 treatment-by-time coefficient was −6.721 points (95% CI −8.820 to −4.625), indicating a greater reduction from baseline with CBT-I. This is a differential-change coefficient, not a standardized effect or the simple endpoint difference. The source's separately reported standardized depression effect should not be paired with a raw-scale interval. Control crossover after week 6 means that week-12 comparisons answer a different question. [6]

The GoodNight primary report also describes a qualifying baseline PHQ-9 ≥10 subgroup with a favorable longitudinal depression result, F(2,166.5)=15.4, p\<.001. A subgroup magnitude or confidence interval was not inferred from that test. Its whole-cohort effect sizes and total sample size are not substituted for subgroup values. [11]

Incremental benefit alongside depression treatment

In the Manber pilot, reported depression-remission proportions were 61.5% with escitalopram plus CBT-I and 33.3% with escitalopram plus control, among 13 and 15 analyzable participants, respectively. The source's one-tailed Fisher test gave p=.13. The numerical difference is compatible with a possible benefit but is not a precise or conclusive remission estimate. [1]

Carney's common-escitalopram comparison did not establish a depression advantage from CBT-I in the reported analysis. The paper gives an observed HAMD17 post-treatment mean of 13.03 for CBT-I plus escitalopram and 11.24 for escitalopram plus hygiene, and a between-group standardized effect magnitude of 0.32. The source does not supply an unambiguous signed adjusted pairwise effect with matching interval, and some reported omnibus F/p pairs appear inconsistent. Those values were not used to manufacture a new precise effect. [2]

Pigeon's depression interaction effect was g=−0.04 at post-treatment (p=.863) and g=0.27 at the three-month follow-up (p=.725). These are depression results; the larger g=−1.03 reported elsewhere in the paper concerns insomnia severity. The trial's small analyzed sample and post-randomization exclusions limit its ability to establish the size or absence of an incremental mood benefit. [3]

Dyrberg's reported adjusted comparison favored CBT-I on HAM-D17 (ANCOVA p=.003), but not HAM-D6 (p=.16). An adjusted difference and confidence interval were not reconstructed from these p values. The scale divergence is clinically relevant because HAM-D17 contains sleep items, while the core-symptom measure offers a different perspective on change. [4]

Blom's depression trajectory did not show a clear incremental benefit of the insomnia component (group-by-time p=.11). The reported observed between-group MADRS-S effect at post-treatment was d=−0.16 (95% CI −0.53 to 0.20), using the source's convention in which this sign favors the depression-plus-placebo comparator; the six-month effect was 0.02 (−0.36 to 0.41). These observed standardized comparisons are distinct from the longitudinal model. [5]

The two retained TRIAD companions contribute information about the parent study and selected trajectories or sleep-duration strata. They were not treated as additional trials or used to reconstruct the overall remission contrast from a primary analysis outside the accepted pool. [12,13]

Comparative evidence with an unverified allocation mechanism

Johnson's report included 106 participants with baseline CES-D ≥16, of whom 29 received the multicomponent intervention and 77 a sleep education/hygiene booklet. Depressive symptoms improved over time in both groups, but the group-by-time interaction was F(1,104)=0.29, p>.05. Thus, the source's favorable within-group description does not establish an additional antidepressant benefit over the booklet. The assignment mechanism and completer selection further limit causal interpretation. [10]

Anxiety and broader clinical comparisons

Chan's week-6 HADS-A treatment-by-time coefficient was −2.770 (95% CI −3.615 to −1.923). This supports reduced anxiety symptoms in its depression-selected population. It does not establish comparable efficacy for every diagnosed anxiety disorder. Within the accepted pool, uncontrolled GAD treatment and sequential active-treatment studies did not supply the target concurrent inactive-control comparison. [6]

The broader-population extension remained clinically informative. GoodNight's whole cohort showed reported between-group depression effect sizes of 0.69 at six weeks and 0.48 at six months; those values concern subclinical-depression entry without current MDD and are not core-subgroup estimates. Its anxiety and longer-term reports belong to the same cohort. Van der Zweerde enrolled insomnia patients across mild-to-severe depressive symptoms, making whole-cohort interpretation broader than the clinical-severity stratum. [11,15,18,19]

The sleep-enhanced transdiagnostic trial added sleep restriction and stimulus-control information to a common anxiety/depression program. Large within-group depression and anxiety changes did not establish incremental mood benefit from the added sleep component. In the rural integrated-treatment trial, CBT-D plus CBT-I versus usual care produced no clear depression group-by-time effect, F(2,39)=0.61, p=.55. Even a positive result in that design would estimate the combined package rather than CBT-I alone. [16,17]

Insomnia, durability and treatment burden

Several reports found sleep improvement alongside mood improvement, although the two outcomes did not always move together. Schuffelen's 12-week adjusted ISI difference was −6.26 (95% CI −7.57 to −4.95), and EPIC's 10-week difference was −4.27 (−5.67 to −2.87). Henry reported a 5.19-point improvement on SCI-8 at 8–10 weeks (4.63 to 5.75); higher SCI-8 scores mean better sleep, unlike ISI. [7–9]

Follow-up findings must retain their control conditions. Schuffelen and Henry provide later comparative depression results, whereas Chan's control group receives treatment after week 6. These data do not justify treating all follow-up effects as sustained benefit over an untreated comparator. [6–9]

Reported tolerability was not uniformly problem-free. In Dyrberg, six of 22 participants who began CBT-I discontinued during treatment: one because of worsening anxiety and five because they could not tolerate sleep-schedule restrictions. Chan reported no adverse events, increased suicidal risk or significant deterioration in primary outcomes; EPIC reported no serious adverse events. Schuffelen reported no adverse events in the intervention group, with reporting initiated by participants contacting the team. Differences in ascertainment and attrition prevent a general claim of absence of harm. [4,6–8]

Appraisal and confidence in the findings

Table 2. Principal limitations affecting interpretation

Important limitations were result-specific. Carney used multiple imputation for primary sleep outcomes but complete-case analyses for depression. Pigeon's small amount of missing questionnaire-item data did not erase the larger participant-level exclusions. EPIC's described missingness sensitivity analyses for co-primary emotional-processing outcomes did not automatically establish robustness of its secondary PHQ-9 result. Blom's masked assessors did not eliminate all concerns for a self-rated depression outcome. [2,3,5,8]

First-assessor RoB 2 judgments were high for the assessed results, frequently because the retained reports left outcome-related missingness or the influence of treatment awareness unresolved. These information-limited judgments are not findings that every effect is demonstrably biased. The combined concerns led to a two-level risk-of-bias downgrade for the direction of PHQ-9 benefit at 8–12 and 22–24 weeks, yielding low certainty. The specific Chan HADS-A result was also rated low certainty. The narrow Manber pilot remission comparison was rated very low because of bias concerns and very serious imprecision. The evidence cannot support a confident claim of absence of important harm. Complete answers, rationales and the scope of each rating are recorded in the reviewer's appraisal worksheets, which are not published with this review. These judgments should be interpreted as structured critical appraisal rather than independent peer review.

Discussion

Within the accepted full-text pool, CBT-I offers a plausible additional route to improving depressive symptoms in adults whose insomnia co-occurs with depression. The most directly interpretable PHQ-9 estimates indicate average reductions of approximately three to four points relative to their respective controls over 8–12 weeks. This describes the reported estimates, not a pooled average or a threshold declaring the benefit clinically important for every individual. [7–9]

The clinical question changes when both arms receive depression treatment. Smaller or inconsistent incremental mood differences may coexist with sleep benefits, and remission can behave differently from symptom-score change. Differences between these trials and trials against waiting or education cannot be attributed solely to therapist versus digital delivery. The comparator, population, concurrent treatment, measurement and analysis all differ. [1–9]

Sleep-related items require particular care. A lower depression total can partly reflect better sleep, but removing sleep items did not remove the reported benefit in Henry's analysis. Conversely, Dyrberg's differing HAM-D17 and HAM-D6 findings warn against assuming that all mood improvements reflect the same clinical domains. Mediation analyses can generate useful hypotheses, but randomized treatment assignment does not itself randomize the mediator or remove all mediator–outcome confounding. [4,9]

This review's main strengths are explicit separation of direct from indirect evidence, attention to overlapping trial families and participant denominators, preservation of discordant findings, and refusal to manufacture precise estimates when the source did not support them. Its limitations are equally important. The evidence pool should not be interpreted as an exhaustive systematic search of all published and unpublished literature. Eligibility and extraction were not performed by two independent reviewers. Some clinically useful findings come from secondary outcomes or selected subgroups. Outcome measures, comparators, follow-up periods and analytic methods vary, and adverse-event ascertainment is inconsistent. These limitations call for calibrated conclusions.

For clinical interpretation, the available evidence favors treating insomnia as a relevant co-occurring problem in its own right. It does not establish that CBT-I replaces indicated depression treatment or that one delivery format is intrinsically superior. Treatment engagement and tolerability, particularly during sleep restriction, deserve attention alongside symptom scales. [1–9]

Practical clinical answer

For an adult with insomnia and depression, the available evidence supports treating persistent insomnia as a treatment target in its own right. CBT-I is an established treatment for insomnia, and several controlled studies in this pool suggest that it can also reduce depressive symptom scores when compared with waitlist, usual care or sleep-hygiene controls.

The evidence is less certain about whether CBT-I increases depression remission, and much less developed for patients selected specifically because they have an anxiety disorder. CBT-I should therefore be viewed as treatment for a clinically important co-occurring insomnia problem that may also help mood or anxiety symptoms, not as a substitute for indicated treatment of depression or anxiety.

Digital CBT-I is supported by several of the larger studies, but the evidence does not establish that digital treatment is superior to therapist-delivered CBT-I. Delivery format should be individualized according to access, preference, clinical complexity, and ability to engage with treatment.

Conclusions

Low-certainty evidence in the accepted pool supports depressive symptom-score reduction with CBT-I in adults with insomnia and qualifying depression. Benefits vary with the clinical comparison and outcome; evidence does not establish dependable additional depression remission or broad anxiety-disorder efficacy. In practical terms, CBT-I may reduce depressive symptom scores by roughly three to four PHQ-9 points relative to inactive insomnia controls at 8–12 weeks (low certainty), with no established incremental benefit on top of active depression treatment and no established effect in diagnosed anxiety disorders.

Transparency and intended use

This manuscript is a physician-authored scoping review of available evidence intended for clinical education and shared decision-making. It is not a clinical practice guideline, consensus statement, Cochrane review, or claim of definitive medical truth. It does not replace individualized diagnosis or treatment.

The review was developed to make the reasoning behind a clinical answer inspectable: what question was asked, which evidence answers it directly, where the evidence is indirect, what the important numerical findings are, and where uncertainty remains. The conclusion is meant to follow the evidence, whatever message would have been more convenient.

Manuscript prepared and last reviewed by Dr. Margarita Krasnova, MD on 2025-12-12.

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Suggested citation

Krasnova M. Evidence Review: CBT-I for Insomnia with Co-occurring Depression or Anxiety margaritakrasnovamd.com. Last reviewed 2025-12-12. Available at: https://margaritakrasnovamd.com/evidence-review/cbti-insomnia-depression-anxiety.html