A Study Of DVS SR In Treatment Of Children And Adolescent Outpatients With MDD: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study Of DVS SR In Treatment Of Children And Adolescent Outpatients With MDD (NCT01372150), a randomized phase 3 study. The primary outcome is Change From Baseline to Week 8 in the Children's Depression Rating Scale, Revised (CDRS-R) Total Score.

2. Clinical Question

The central statistical question is whether the observed mean changes differ between each active arm and placebo, and how much uncertainty surrounds those differences. The registry reports adjusted mean changes for the arms and sponsor analyses using repeated-measures models. Unadjusted recalculations from posted summaries offer a separate, simpler comparison; they are not the same analysis as the sponsor’s model.

The active reference arm gives context for interpreting the trial, but the record does not establish an equivalence or noninferiority question. It describes fluoxetine as an active control for assay sensitivity and lists superiority-or-other analyses. The statistical results should therefore be read as estimates and uncertainty intervals for the stated comparisons, not as proof that treatments are equivalent or that a treatment has a particular clinical effect.

3. Trial Design

The registry describes a Phase 3, randomized, triple-masked, parallel-group study with placebo control and fluoxetine reference. It was multicenter and evaluated efficacy, safety, and tolerability of DVS SR in children and adolescent outpatients with major depressive disorder. The study status is completed, and the registered enrollment is 340.

Three drug arms are listed: DVS SR, fluoxetine, and placebo. Fluoxetine is described as an active control for assay sensitivity. The primary outcome was the change from baseline to Week 8 in CDRS-R total score. The registry lists the analysis population for that outcome as the ITT population, defined by randomization, receipt of at least 1 dose, a baseline primary efficacy assessment, and at least one post-baseline primary efficacy assessment.

The outcome summaries give analysis counts of 99 for placebo, 101 for fluoxetine, and 99 for DVS SR. These are the counts attached to the primary outcome summaries and should not be confused with the registered enrollment. The record does not report the trial’s original sample-size justification, the allocation ratio, or the full set of protocol assumptions used when planning enrollment.

The registry lists secondary outcomes covering CGI-S change and CGI-I status or response at several assessments. It also reports serious and other adverse-event counts. Details such as the precise study-drug dosing regimen and the full schedule of safety assessments are not reported in the registry record. The design description establishes the broad comparison structure, but does not by itself answer how missing observations, multiplicity, or interim monitoring were handled.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention-To-Treat (ITT) Population - included all randomized participants who received at least 1 dose of study drug, had a baseline primary efficacy assessment, and had at least one post-baseline primary efficacy assessment.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Safety population - included all randomized participants who received at least 1 dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline to Week 8 in the Children's Depression Rating Scale, Revised (CDRS-R) Total Score, measured over Baseline and Week 8.

The primary endpoint is change from baseline to Week 8 in the Children’s Depression Rating Scale, Revised (CDRS-R) total score. The record describes it as a clinician-rated, interview-based measure drawing on information from the child and a parent or guardian. It assesses 17 symptom areas. When informants’ responses disagreed, the most impaired rating from a valid informant was used.

Each item is rated on a 7-point scale, and the total is the sum of the 17 items, with a range from 1 to 119. Higher scores indicate greater impairment. A negative change therefore represents a lower score at Week 8 than at baseline, which is directionally consistent with reduced measured impairment. This describes the scale’s direction; it is not, by itself, a judgment about clinical importance.

A continuous total score can capture changes across the range of measured severity rather than reducing each participant’s result to a yes-or-no response category. The registry reports adjusted mean change and standard error for the arms. Comparing mean changes can summarize the average shift in this measure, while the interval around a between-arm estimate conveys uncertainty about the size and direction of the contrast.

The record does not report a threshold for a clinically important CDRS-R change. Thus the numerical differences should be interpreted as score differences, not automatically as meaningful improvement for an individual participant.

7. Results Posted in the Registry

• Fluoxetine: mean -24.79 versus -23.07 on control; difference -1.72 (95% CI -4.98 to 1.54), standardized effect d = -0.15; z-test p = 0.301.
• DVS SR: mean -22.61 versus -23.07 on control; difference 0.46 (95% CI -2.80 to 3.72), standardized effect d = 0.04; z-test p = 0.782.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change From Baseline to Week 8 in the Clinical Global Impression of Severity (CGI-S) Score

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Fluoxetine: mean -1.88 versus -1.71 on control; difference -0.17 (95% CI -0.50 to 0.16), standardized effect d = -0.14; z-test p = 0.316.
  • DVS SR: mean -1.70 versus -1.71 on control; difference 0.01 (95% CI -0.31 to 0.33), standardized effect d = 0.01; z-test p = 0.951.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fluoxetine and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DVS SR and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend assessment beyond the primary CDRS-R measure. They include change in CGI-S and CGI-I ratings or response at listed assessment times. The available numeric secondary summaries cover CGI-S change; the registry lists CGI-I outcomes, but detailed numerical results for those outcomes are not reported in the registry record.

The CGI-S comparison pattern is broadly consistent with the primary endpoint in that the arm contrasts are small relative to their uncertainty, and the sponsor-reported intervals include zero. This offers a related measure of severity, but it does not independently resolve uncertainty in the primary comparison. The CGI-I outcomes concern improvement categories and responses, so they measure a different aspect of clinical assessment; their results cannot be inferred from the continuous CGI-S values or the CDRS-R findings.

Secondary analyses generally carry less weight than the prespecified primary comparison when many outcomes or assessment times are examined. Each additional test creates more opportunity for a seemingly notable result to arise by chance. Appropriate interpretation depends on whether multiplicity was addressed, which outcomes were prespecified, and how missing observations were handled. Those details are not reported in the registry record. Accordingly, secondary findings should be treated as supportive or exploratory rather than as a replacement for the primary result, particularly when their numerical results and adjustment procedures are incomplete.

The registry states that multiple analyses are posted, but the count alone does not reveal the testing hierarchy or adjustment strategy. The available secondary information therefore supports a cautious overall reading, not a claim that every listed secondary measure followed the same pattern or reached a particular conclusion.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Change From Baseline to Week 8 in the Clinical Global Impression of Severity (CGI-S) Score
• Percentage of Participants by Clinical Global Impression Improvement (CGI-I) Score at Weeks 1, 2, 3, 4, 6, and 8
• Percentage of Participants With a CGI-I Response Defined as a Score of 'Very Much Improved' or 'Much Improved'

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it is a score and its change over time, not an event count. The record reports means and standard errors for each arm. A mean describes the average observed change in the analyzed group; a standard error describes the precision of that estimated mean. It is not the same as the spread of individual participant scores.

What does a mean difference represent?

A between-arm mean difference compares the average changes in two arms. The recalculated comparisons use placebo as the reference and express the result as the active-arm mean minus the placebo mean. A negative estimate means the active-arm change is more negative under that convention; a positive estimate means it is less negative. The sign depends on which arm is subtracted from which, so the direction of the contrast must be checked before comparing estimates from different analyses.

The recalculated estimates are unadjusted comparisons derived from the posted arm summaries. They do not reproduce the sponsor’s model, which is reported as a mixed-effects model for repeated measures for fluoxetine and as MMRM for DVS SR. Repeated-measures models analyze measurements collected over time and can account for their within-participant relationship. In general, modeling repeated observations can use information from multiple assessment times rather than treating a single endpoint summary as the whole analysis. The registry record does not describe the model’s covariance structure, covariates, estimation details, or missing-data assumptions, so those features cannot be assessed from the reported method label alone.

Why do confidence intervals matter?

A confidence interval expresses the uncertainty around an estimated contrast under the method used to calculate it. An interval that includes zero is compatible with no mean difference, as well as with values on either side of zero within the interval. It is not evidence that the true difference is exactly zero. The width of an interval indicates how precisely the estimate is determined: a narrower interval gives a more concentrated range of values compatible with the analysis, while a wider interval leaves more uncertainty.

The sponsor reports 95% confidence intervals for the repeated-measures comparisons. The recalculated intervals are also presented as uncertainty ranges for the unadjusted comparisons. Since these methods differ, small differences between their estimates or interval limits are not inherently contradictory. A model-based estimate may reflect the model and available repeated observations, whereas a summary-statistic calculation is limited to the posted group summaries.

What does a p-value say?

A p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The reported p-values for the primary comparisons are not small by conventional thresholds, but a p-value alone is not a sufficient summary. The estimated differences and their confidence intervals show the range of uncertainty and possible directions more directly.

The registry labels the sponsor analyses as superiority-or-other and provides no noninferiority or equivalence margin. Therefore, a lack of a small p-value cannot be interpreted as demonstrating equivalence, and an active-control comparison cannot be recast as a noninferiority conclusion without the required design and analysis details.

How should repeated-measures results be distinguished from the recalculation?

The sponsor’s reported analyses use repeated-measures methods and report differences in final values. The recalculations use the posted mean changes and pooled standard deviations to obtain simple, unadjusted comparisons. The latter support an accessible check on the magnitude and direction of the contrast but do not adjust for repeated observations or any covariates. The record marks the discrepancy indicator as false, but that does not make the methods interchangeable; they remain different estimands and calculations as described in the registry.

More generally, statistical analysis depends on the population included, the timing and pattern of measurements, and assumptions about data not observed. Those details affect what the estimate represents and how uncertainty is quantified. The registry identifies the primary analysis population and the broad model type, but further protocol and model specifications are not reported in the registry record. Statistical interpretation should therefore stay with the comparisons and methods explicitly described rather than infer unreported modeling choices.

11. Confidence Intervals and Precision

The primary unadjusted recalculation for fluoxetine versus placebo is -1.72, with a 95% confidence interval from -4.977 to 1.537. The interval crosses zero, covering values that favor either direction under the treatment-minus-placebo convention. The DVS SR versus placebo estimate is 0.46, with a 95% confidence interval from -2.797 to 3.717; this interval also crosses zero and allows for effects in either direction.

The sponsor’s model-based intervals likewise include zero: 1.71 with a 95% confidence interval from -1.06 to 4.48 for fluoxetine versus placebo, and -0.47 with a 95% confidence interval from -3.23 to 2.30 for DVS SR versus placebo. The signs reflect the sponsor’s reported contrast direction and should be read with that in mind. These model-based estimates and recalculated estimates are not identical analyses.

Confidence intervals are useful because they show both the estimated direction and the range of values that remain compatible with the data and method. Here, the intervals do not isolate a single direction of effect. That makes the estimates imprecise for distinguishing a difference from no difference. The intervals do not establish that the arms are equivalent: equivalence requires a prespecified margin and an analysis designed to evaluate that claim, and such a margin is not reported in the registry record.

Precision also concerns clinical interpretation. The record does not state what difference in CDRS-R score would be clinically important, so the intervals cannot be classified against such a threshold. They describe statistical uncertainty in score differences, not certainty about the experience or outcome of any individual participant.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size illustrations concern future planning based on the observed contrasts, not the original trial’s design justification. Because the outcomes are continuous, the entries are participants per arm, rather than total event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original trial’s own sample-size assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm estimated to give an 80% chance of detecting the specified effect under those planning assumptions, if that effect and assumptions hold. The 90% power column uses a higher target chance of detecting that same specified effect, and therefore generally requires more participants per arm. These are planning illustrations, not observed power.

Rows for planning for 75% or 50% of the observed effect consider smaller target differences than the full observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the same assumptions. The very large figures in some rows reflect the small observed contrasts used as the starting point for those illustrations; they are not evidence that the completed study enrolled the numbers in those rows.

These calculations are simplified and depend on the stated assumptions. They do not establish what sample size would be appropriate under a different model, allocation, outcome, or target effect. The illustrations should be read as sensitivity to effect size and power target, not as a retrospective measure of how likely the completed trial was to find a result.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -1.720; pooled standard deviation σ = 11.750.
2. n = 2 × (1.96 + 0.842)² × 11.750² / -1.720² = 732.5, rounded up to 733 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -1.72                      # observed difference in means
sigma <- 11.7496947735985                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1372150)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 733 (80% power), 981 (90% power)
 75% of observed effect: n per arm = 1,303 (80% power), 1,744 (90% power)
 50% of observed effect: n per arm = 2,931 (80% power), 3,923 (90% power)
power.t.test: 733.5 
Simulated power at n = 733 per arm: 0.798 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry’s sponsor analyses use repeated-measures models and report mean differences in final values. For fluoxetine versus placebo, the sponsor reports 1.71, with a 95% confidence interval from -1.06 to 4.48 and p = 0.226. For DVS SR versus placebo, the reported estimate is -0.47, with a 95% confidence interval from -3.23 to 2.30 and p = 0.739. Both intervals include zero.

The recalculated comparisons are unadjusted and use the posted change-score summaries. Their estimates are -1.72 for fluoxetine versus placebo and 0.46 for DVS SR versus placebo. The apparent sign reversal is explained by the direction of subtraction: the recalculations are expressed as active arm minus placebo, while the sponsor’s reported values correspond in sign to the reverse contrast. The estimates are close in magnitude, but their methods and reported quantities are not interchangeable.

The sponsor’s model-based results are the analyses reported for the trial; the recalculations are a separate statistical check using summary data. The record does not provide enough model detail to reconstruct the repeated-measures analyses independently. No discrepancy is flagged in the registry record. Neither set of comparisons supports a claim of equivalence, since no equivalence margin is reported.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists several secondary outcome measures and multiple analyses, so multiplicity is relevant: testing many outcomes, time points, or contrasts can increase the chance of at least one apparently unusual result. The registry record does not report whether a family-wise error procedure, hierarchical testing plan, or other multiplicity adjustment was used. The reported p-values should therefore not be assumed to have been adjusted, and an isolated secondary result would need cautious interpretation.

The primary endpoint’s analysis population is explicitly defined. It includes randomized participants who received at least 1 dose, had a baseline primary efficacy assessment, and had at least one post-baseline primary efficacy assessment. This is the registry’s ITT definition, but it excludes randomized participants who do not satisfy those analysis-population requirements. The number excluded for each reason and the impact of those exclusions are not reported in the registry record.

The sponsor’s primary analyses are described as mixed-effects modeling for repeated measures or MMRM. In general, repeated-measures methods can use observations collected at multiple visits, but their interpretation depends on model specification and assumptions about missing data. The registry record does not report the missing-data assumptions, the extent or pattern of missing measurements, sensitivity analyses, or the detailed model specification. It is therefore not possible to determine from the record alone how robust the estimates are to departures from those assumptions.

Interim analyses, stopping rules, and the protocol’s full statistical analysis plan are not reported in the registry record. Their absence from the record is not evidence that such procedures were or were not used. These reporting gaps limit assessment of prespecification and analysis flexibility, and should be kept separate from the numerical results that are posted.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: suicidal ideation (0.9%), suicide attempt (0.9%), disinhibition (0.9%).

The registry reports serious adverse events for groups at risk of 112 in placebo, 112 in fluoxetine, and 115 in DVS SR. Serious adverse events are recorded for 0 in placebo, 2 in fluoxetine, and 2 in DVS SR. The listed serious-event terms are suicidal ideation, suicide attempt, and disinhibition, each reported as 0.9%. The record does not assign those term percentages to a particular arm in the listed summary.

For other adverse events, the registry reports counts of 44 for placebo, 39 for fluoxetine, and 47 for DVS SR, with the corresponding groups at risk stated as 112, 112, and 115. These counts are descriptive; the registry record does not provide enough detail to interpret severity, timing, duration, or causal attribution. Death counts are not reported in the registry record.

Adverse-event counts should be read as safety summaries, not as proof that an event was caused by study drug or that one arm is safer. The record does not report the follow-up window for these summaries or provide a detailed comparative safety analysis. The group-at-risk figures are specific to the safety reporting and differ from the primary efficacy analysis counts, so they should not be substituted for the primary endpoint population.

17. What the Result Does, and Does Not, Mean

The posted primary results show decreases in mean CDRS-R scores from baseline to Week 8 in all three arms. The between-arm estimates are comparatively close to zero, and both the unadjusted recalculated intervals and sponsor-reported intervals include zero. This means the reported analyses do not clearly distinguish the active arms from placebo on the primary score change, while still allowing uncertainty about the direction and size of any difference.

That finding is not proof that the treatments are equivalent, and it is not proof that there is no effect. Equivalence requires a margin defining how small a difference must be to count as equivalent, together with a suitable analysis; such a margin is not reported. Nor does a nonsignificant result establish that the study had no capacity to detect any effect. The sample-size illustrations are planning calculations, not observed power.

The results are specific to the registry-defined analysis population, the CDRS-R score, and the baseline-to-Week 8 comparison. They do not establish what happened to every randomized participant, because the primary analysis population required receipt of study drug and primary efficacy assessments. They also do not settle outcomes measured by the secondary CGI-I endpoints, for which numerical findings are not reported in the registry record.

Statistical uncertainty is not the same as clinical importance. The record does not state a clinically important score difference, so it cannot show whether any value within the confidence intervals would matter to patients or clinicians. In addition, safety counts are descriptive and do not establish causation or comparative safety. The strongest grounded conclusion is limited: the posted primary comparisons have estimates near zero relative to their uncertainty, and the registry does not provide evidence sufficient to claim equivalence or a clinically meaningful difference.

18. Why This Trial Matters Statistically

This trial is statistically informative because it combines a placebo comparison with an active reference arm and reports both arm-level score changes and model-based contrasts. The design makes the role of the comparator explicit: fluoxetine was included as an active control for assay sensitivity, while placebo served as the control in the posted comparisons. The results can therefore be examined as estimates within a randomized, parallel-group framework without confusing an active-control purpose with a demonstrated equivalence claim.

The record also illustrates why the estimate alone is not the whole result. A mean difference must be read alongside its confidence interval, the direction of subtraction, and the method used. Here, the sponsor’s repeated-measures analyses and simple unadjusted recalculations have different specifications; their contrasts are similar in magnitude but should not be treated as identical calculations.

Planning illustrations based on the observed effects show how sample-size requirements are sensitive to the target effect and desired power. Because the observed between-arm differences are small, planning for still smaller effects leads to large per-arm requirements under the stated assumptions. This is a planning lesson, not a claim about the trial’s original rationale or observed power.

Finally, the record highlights the importance of transparent reporting. Definitions of the analysis population are useful, while incomplete information about multiplicity, missing data, and model details limits assessment of robustness. These distinctions help readers separate what the posted estimates show from what remains unresolved.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the original sample-size justification, the allocation ratio, detailed randomization procedures, or full protocol assumptions. Although the design is described as randomized and triple-masked, the specific roles masked and any procedures for maintaining masking are not detailed in the record.

The primary analysis population requires a baseline and at least one post-baseline efficacy assessment as well as receipt of study drug. The registry does not report how many randomized participants did not meet that definition or give a comparison of included and excluded participants. Missing-data patterns, model assumptions, and sensitivity analyses are also not reported, limiting evaluation of the repeated-measures estimates.

The registry reports the broad model labels but not the full model specification, covariates, covariance structure, or adjustment details. It does not state whether multiplicity was controlled across secondary outcomes and repeated assessment times. Numerical CGI-I findings are not reported in the registry record, so the listed CGI-I outcomes cannot be assessed from the available results. A clinically important difference threshold for CDRS-R is also not reported.

The adverse-event summary does not provide a detailed account of timing, seriousness criteria, attribution, or follow-up window. The listed serious-event percentages are not linked to individual arms in the summary. As a result, the safety figures support description of reported counts but not a comprehensive comparative safety assessment. These limitations concern the detail available in the registry record and should not be mistaken for evidence that the unreported procedures or information were absent from the complete study documentation.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study Of DVS SR In Treatment Of Children And Adolescent Outpatients With MDD — NCT01372150.
• Registry record last updated 2019-01-15; status last verified 2019-01.
• Results first posted 2015-11-20.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed Phase 3 randomized, triple-masked, parallel-group study of DVS SR in children and adolescent outpatients with major depressive disorder. The arms were DVS SR, fluoxetine, and placebo, with fluoxetine designated as an active control for assay sensitivity. Registered enrollment was 340.

The primary outcome was change from baseline to Week 8 in CDRS-R total score. The posted arm means decreased in all groups. The sponsor’s repeated-measures comparisons and unadjusted recalculations both have confidence intervals that include zero. The record does not establish equivalence or report a clinically important difference threshold.

Secondary measures include CGI-S and CGI-I outcomes; detailed numeric results for CGI-I are not reported in the registry record. Safety summaries report serious and other adverse-event counts, but do not provide a full comparative safety analysis. Important details concerning multiplicity, missing data, and the original sample-size plan are not reported in the registry record.