Efficacy of Vortioxetine (Lu AA21004) in the Prevention of Relapse of Major Depressive Episodes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy of Vortioxetine (Lu AA21004) in the Prevention of Relapse of Major Depressive Episodes (NCT00596817), a randomized phase 3 study. The primary outcome is Relapse Within First 24 Weeks of the Double-blind Period Based on a MADRS Total Score >=22 or an Unsatisfactory Treatment Effect (Lack of Efficacy) as Judged by the Investigator.

2. Clinical Question

This is a conditional question about maintaining a response among patients who had already responded during open-label vortioxetine treatment. It is not a comparison of starting vortioxetine versus starting placebo in an unselected group of patients with major depressive disorder. Selection into the double-blind phase after response is central to interpreting the population to which the comparison applies.

3. Trial Design

The registry describes a Phase 3, randomized, double-blind, parallel-group, placebo-controlled trial sponsored by H. Lundbeck A/S. It lists an enrollment of 639 and a completed status. The registry dates the study start to 2007-12 and primary completion to 2009-09. Those figures describe the registered study overall, not the number included in each primary double-blind analysis.

The study had an open-label treatment period followed by a double-blind relapse-prevention period. The stated purpose was to evaluate vortioxetine for preventing relapse among patients who responded to open-label vortioxetine. During the double-blind comparison, the registered groups were placebo and vortioxetine 5 or 10 mg. The primary endpoint covered the first 24 weeks of the double-blind period. The record also lists outcomes assessed over the entire double-blind period and outcomes assessed at Week 24.

Random allocation and double masking are features of the double-blind comparison as described in the registry. The registry record does not report the randomization sequence method, allocation concealment procedures, masking procedures, the rationale for the dose group, or the duration of the entire double-blind period beyond the stated endpoint timeframes. These details should not be inferred from the general design labels.

The overall enrollment was 639, while the primary endpoint results list 192 participants for placebo and 204 for vortioxetine. The difference between overall enrollment and these analysis counts is not explained in the registry record. It is consistent with the stated sequence of open-label treatment and a subsequent double-blind comparison, but reasons why particular participants did or did not contribute to the primary analysis are not reported. The registry identifies the primary analysis population as FAS without giving its operational definition.

Because entry into the randomized phase followed response to open-label vortioxetine, the design addresses relapse prevention in that selected group. It does not directly estimate outcomes for all patients who might begin treatment. This distinction follows from the stated study sequence and is important when considering the scope of the findings.

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.

Before assignment: The study consisted of two consecutive periods: a 12-week open-label treatment period with Vortioxetine and a double-blind, fixed-dose, placebo-controlled treatment period of at least 24 weeks.

Open-label Period

Reasons for not completing this period:

Open-label Period to Double-blind Period

Reasons for not completing this period:

Double-blind Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS

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: The total number of patients under Baseline Measures is not 1035 as automatically calculated, but 639 as stated in the "Open-label Period (APTS)" column and 396 in the "Double-blind Period (FAS)". The "Total" column of each Baseline Measure is Double-blind Period (FAS).

6. Primary Endpoint

The registry lists the primary outcome as Relapse Within First 24 Weeks of the Double-blind Period Based on a MADRS Total Score >=22 or an Unsatisfactory Treatment Effect (Lack of Efficacy) as Judged by the Investigator, measured over Within first 24 weeks of the double-blind period.

The primary endpoint was relapse within the first 24 weeks of the double-blind period. The registry defined relapse as a MADRS total score of 22 or more, or an unsatisfactory treatment effect judged by the investigator as lack of efficacy. It reported the percentage of patients who relapsed in each group and a Cox-model hazard ratio comparing the groups.

The MADRS is a 10-item depression rating scale. Each item is rated from 0, indicating no symptom, to 6, indicating a severe symptom; the total score ranges from 0 to 60, with higher scores indicating more severe symptoms. The registry says ratings are based on a clinical interview covering the last 7 days. The endpoint therefore combines a prespecified score threshold with an investigator judgment about inadequate treatment effect. The record does not report how often each component independently determined relapse.

Time-to-event analysis is generally useful when the timing of an event matters and participants may have different lengths of observation. A hazard ratio compares event rates over follow-up under the model; it is not the same quantity as a difference between the percentages who experienced an event. In this trial, the relapse percentages provide a direct description of the observed group proportions, while the Cox-model result summarizes the relative event timing over the specified period. Neither measure alone describes every participant’s course or the severity and duration of symptoms before an endpoint event.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a count-type endpoint expressed as the percentage of patients who relapsed. The registry also reports a Cox-model hazard ratio. These summaries complement one another: the group percentages describe the proportion with a recorded relapse during the stated interval, and the hazard ratio uses information about when events occurred. A hazard ratio is a relative measure of event rates over time under the model; it should not be interpreted as a simple ratio of the two percentages or as a direct probability for an individual patient.

In general, a Cox model compares hazards while accounting for the time until an event and for participants whose event is not observed during follow-up. Its interpretation relies on model assumptions, including an assumption about how the relative hazards behave over time. The registry names the Cox model but does not report diagnostics, the handling of censoring, or an assessment of whether model assumptions were met. Those details are therefore not reported in the registry record.

The primary estimate is reported with a 95% confidence interval. In general, a confidence interval gives a range of estimates compatible with the data and model at the stated confidence level; it is not a range containing a specified proportion of individual outcomes. For a hazard ratio, the reference value for no relative difference is 1. The interval reported for the primary comparison lies above that reference. The p-value of 0.004 is a measure of how incompatible the observed result is with the model’s null hypothesis under its assumptions, not a measure of the size or importance of an effect.

The primary endpoint is defined by either a MADRS total score of 22 or more or an investigator’s judgment of unsatisfactory treatment effect because of lack of efficacy. Such a combined definition can capture more than one operational route to classifying relapse. It also means the overall estimate depends on the combined endpoint as defined, rather than on either component alone. The record does not report separate results for the score criterion and the investigator judgment, nor does it detail adjudication procedures.

The continuous secondary outcomes report changes in scale scores and include standard errors. In general, a mean change describes the average observed change in a group; a standard error describes uncertainty in the estimated mean, rather than the spread of individual participants’ scores. A mean difference compares group averages. The registry’s own analyses for these outcomes are ANCOVA models, reported as mean differences in final values. The record does not report the covariates used in those models, so the exact adjustment cannot be reconstructed from the registry record.

Some descriptive comparisons are recalculated from posted summary statistics and are unadjusted. They are not substitutes for the sponsor’s reported analyses. A recalculation from group means and standard errors does not reproduce an ANCOVA that may account for baseline values or other model terms. The registry record does not show that the recalculations were the prespecified analysis. For this record, the sponsor’s reported analyses take precedence when describing the trial’s own statistical results; there is no stated discrepancy between those analyses and the posted summaries.

Standardized effect measures can express a mean difference relative to a measure of variability, making results across different scales easier to compare in broad terms. They do not remove limitations in the underlying study design, and their interpretation depends on how variability is estimated. The registry’s posted continuous summaries include standard errors, while some descriptive recalculations use pooled variability. These are distinct ways of summarizing uncertainty and scale, and they should not be treated as interchangeable with the trial’s adjusted analysis.

Planning illustrations based on an observed effect are not observed power. In general, sample-size planning asks how many participants per arm would be needed to detect a chosen effect under specified assumptions. The registry’s planning assumptions describe a two-sided significance level of 0.05, equal allocation, and a normal approximation, with scenarios using a stated fraction of the observed effect. Such illustrations depend on those assumptions and on the observed effect used as their starting point. They do not establish the trial’s original design target, because the trial’s own sample-size justification is not reported in the registry record.

Over-dispersion is a general issue for count data: if variability exceeds what a simple model assumes, standard errors and confidence intervals may be too narrow. It is not possible to assess that issue for the primary endpoint from the listed group percentages alone. The registry reports a Cox model rather than a count regression model, and does not provide diagnostics that would establish whether its assumptions fit the data. This general point is not a claim that over-dispersion occurred in this study.

The registered primary analysis population is FAS, but the record does not define the acronym or state which randomized participants were included under that label. The primary group counts are smaller than the overall enrollment. Without the analysis-population definition and accounting for participants who were excluded, did not enter the double-blind period, or lacked an endpoint assessment, the scope of the analyzed population cannot be reconstructed fully. The record also does not report the missing-data method, sensitivity analyses, or whether the analyses followed an intention-to-treat principle.

There are multiple secondary outcomes, including relapse over the entire double-blind period, score changes, response, remission, and functioning. When many outcomes are tested, the chance of at least one apparently notable result can increase if each is interpreted without adjustment. In general, multiplicity procedures control or describe that issue, but the registry record does not report whether any procedure was prespecified or applied. Consequently, unadjusted secondary p-values should not carry the same confirmatory weight as the designated primary analysis.

10. Analyses Reported by the Sponsor

The sponsor’s primary analysis is a Cox-model comparison. It reports a hazard ratio of 2.01, a 95% confidence interval from 1.26 to 3.21, and p = 0.004 for the listed comparison of placebo and vortioxetine. The posted relapse percentages are 26.0% for placebo and 13.2% for vortioxetine 5 or 10 mg, in the same direction as that model-based comparison. The model result and the percentages are not identical measures: one uses event timing, while the other reports group proportions.

For the continuous secondary outcomes, the sponsor reports ANCOVA mean differences and confidence intervals. Those adjusted model results are the trial’s own analyses. Separate unadjusted recalculations from posted means and standard errors are descriptive checks, not replacements for ANCOVA. They may differ because the registry’s reported model can account for information that is not encoded in the simple group summaries. The record does not give the ANCOVA covariates or full model specification.

No discrepancy is flagged between the posted summaries and the sponsor’s analyses. The sponsor’s analyses therefore provide the primary basis for describing the trial’s inferential results. Recalculated estimates, where available, should be read as unadjusted illustrations rather than as corrections to the registered analysis.

11. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint and lists eight secondary outcomes. It does not report whether the secondary outcomes were tested under a prespecified hierarchy, whether p-values were adjusted for multiple comparisons, or whether any gatekeeping procedure was used. That information is not reported in the registry record. Without it, the secondary p-values cannot be interpreted as if each were a standalone confirmatory test with no multiplicity concern.

Multiplicity matters because testing many outcomes can increase the chance that at least one result appears persuasive by chance alone. This general issue does not mean that any particular result is false; it means that the strength of evidence is harder to assess when the testing strategy is unknown. The primary endpoint has a distinct registered role, while the secondary findings offer additional context with less secure inferential standing when adjustment procedures are not documented.

The record identifies the primary population as FAS but does not define that term or describe exactly who was included. It gives the primary endpoint group counts and varying counts for the secondary outcomes, but not a participant flow or reasons for non-inclusion. The missing-data approach, imputation method, handling of withdrawals, and sensitivity analyses are not reported in the registry record. It is therefore not possible to assess from this record whether missing outcomes could have altered the estimates or how robust the results are to alternative assumptions.

The distinction between the overall enrollment of 639 and the smaller double-blind analysis counts is relevant to interpretation. The study summary indicates that the double-blind phase followed open-label vortioxetine treatment and response, but the record does not provide the number progressing at each stage or reasons for not proceeding. No conclusion about the cause of that difference should be drawn from the counts alone.

The record also does not report interim analyses, stopping rules, the sample-size justification, or a detailed statistical analysis plan. Those elements are important for evaluating whether analyses and decision thresholds were established before outcomes were known. Their absence from the registry record does not establish that they were absent from the study conduct; it means that they cannot be evaluated from the registered information.

12. 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: road traffic accident (1.0%), abortion incomplete (0.8%), cholelithiasis (0.5%), influenza (0.5%), nasopharyngitis (0.5%).

The adverse-event figures distinguish the open-label period from the double-blind period. In the open-label period, 14 of 639 participants were reported with serious adverse events, and 337 of 639 were reported with other adverse events. In the double-blind period, the placebo group had 6 of 192 participants with serious adverse events and 73 of 192 with other adverse events; the vortioxetine 5 or 10 mg group had 7 of 204 with serious adverse events and 79 of 204 with other adverse events.

These are counts of participants affected, not a statistical comparison of risk. The open-label and double-blind figures concern different study periods and populations, so the open-label counts should not be compared directly with either randomized group as though they were parallel arms. The registry does not provide a comparative inferential analysis for these adverse-event figures. Death counts are not reported in the registry record.

The record lists serious adverse-event terms with percentages, including road traffic accident, incomplete abortion, cholelithiasis, influenza, nasopharyngitis, and upper respiratory tract infection. These entries describe reported terms; they do not establish that a study treatment caused an event. The registry record does not provide enough detail in these summaries to assess event relatedness, timing, recurrence, or the clinical context of each case. These figures should be read as descriptive safety reporting rather than as a complete assessment of comparative safety.

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

The posted primary data show a lower relapse percentage in the vortioxetine 5 or 10 mg group than in the placebo group during the first 24 weeks of the double-blind period. The sponsor’s Cox-model result also indicates a difference between the groups under that model, with a confidence interval that does not include the no-difference value for a hazard ratio. These findings describe the registered comparison among patients who responded to open-label vortioxetine and entered the double-blind phase.

They do not establish what would happen among all people with major depressive disorder, including those who did not respond to open-label treatment. The study question is conditional on prior response and does not compare initial treatment choices in an unselected population. The result also does not describe outcomes beyond the stated follow-up or establish what happens with other doses, other comparators, or other treatment settings not listed in the record.

A group-level percentage is not an individual prediction. The comparison does not mean that every participant in one group relapsed or that no participant in the other group did. The hazard ratio likewise summarizes relative event timing under a model; it does not give the probability that a particular person will relapse. The registry does not report separate results for the score-based and investigator-judgment components of the composite endpoint, so their individual contributions cannot be inferred.

Statistical evidence of a group difference is not, on its own, a measure of clinical importance. The registry’s estimates and uncertainty help quantify the observed comparison, but they do not define what magnitude of difference would matter to patients or clinicians. Nor do the results establish a mechanism, guarantee an outcome, or account for every potential benefit and harm. The safety summaries are descriptive and do not replace a full comparative safety analysis.

The most defensible reading is therefore bounded: the registered analysis reports fewer relapses in the vortioxetine group than the placebo group among the analyzed double-blind participants, with a model-based estimate favoring the vortioxetine group in the stated comparison. The result must be interpreted in light of the selected population, composite endpoint, unreported analysis details, and the limits of registry-level information.

14. Why This Trial Matters Statistically

This trial is statistically notable for the way its design separates treatment response from relapse prevention. Participants first received open-label vortioxetine, and the randomized, double-blind comparison addressed subsequent relapse among responders. That design asks a narrower question than a conventional treatment-initiation comparison, and the population definition is essential to understanding what the resulting estimate represents.

The primary outcome also combines a scale threshold with investigator judgment. Composite endpoints can be useful when more than one criterion can indicate an event, but their overall estimate may conceal which component drives the result. The registry does not report component-specific results, making the combined endpoint the available basis for interpretation.

The analysis illustrates why percentages and time-to-event estimates should be read together but not conflated. The relapse percentages give an accessible account of the observed proportions; the Cox-model hazard ratio incorporates event timing under its assumptions. Reporting both helps describe the result, while model details and diagnostics remain important for judging how well the estimate is supported.

The record also highlights the distinction between the trial’s sponsor-reported analysis and unadjusted recalculations from summary statistics. The sponsor’s ANCOVA analyses are not reproduced by simple comparisons of group summaries. Similarly, planning illustrations based on observed effects are not evidence of the original design’s power or sample-size rationale. Recognizing these distinctions prevents descriptive calculations from being mistaken for the trial’s prespecified inference.

Finally, the registry has meaningful reporting gaps about missing data, population definitions, multiplicity, and the statistical plan. These are not reasons to discard the reported result, but they limit how completely its robustness can be assessed. In clinical research, a statistically interpretable estimate depends not only on its numerical value but also on who was analyzed, how outcomes were defined, and how uncertainty and multiple analyses were handled.

15. 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 registered population is selected by response to open-label vortioxetine before the double-blind comparison. Consequently, the primary estimate does not directly address patients who did not respond during that period or patients beginning treatment without prior exposure. The registry gives the overall enrollment and the primary analysis counts but does not provide a full account of progression from the open-label phase into the randomized phase.

The primary endpoint combines a MADRS threshold with investigator-assessed lack of efficacy. The record does not separate results for those criteria, describe adjudication, or report how overlapping criteria were handled. The combined result therefore cannot show whether one component contributed more than the other. The record also does not report the distribution of relapse times or supporting model diagnostics.

The primary population is labelled FAS, but its definition is not reported in the registry record. The record does not describe exclusions, missing outcome data, imputation, withdrawal handling, or sensitivity analyses. These omissions limit assessment of whether the analysis population and assumptions about missingness could affect the estimate. Secondary outcome sample sizes vary, and the record does not explain the variation.

The registry reports a Cox model for the primary endpoint and ANCOVA for continuous secondary outcomes, but does not give a complete statistical analysis plan. Model covariates, model diagnostics, interim analyses, and stopping rules are not reported in the registry record. The record also does not describe a multiplicity adjustment for the secondary outcomes. Therefore, secondary findings should be treated more cautiously than the designated primary analysis.

Finally, the adverse-event summaries are descriptive, and the record does not report a comparative statistical analysis or treatment-relatedness details for the listed events. The registry record does not provide enough information to evaluate all aspects of safety, the clinical importance of the observed outcome difference, or how broadly the findings apply beyond the studied responder population.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Efficacy of Vortioxetine (Lu AA21004) in the Prevention of Relapse of Major Depressive Episodes — NCT00596817.
• Registry record last updated 2014-03-31; status last verified 2014-02.
• Results first posted 2014-03-31.
• 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.

19. Record Summary

NCT00596817 is a completed Phase 3 randomized, double-blind, parallel-group, placebo-controlled relapse-prevention study sponsored by H. Lundbeck A/S. The registry lists 639 participants overall and describes a double-blind comparison of placebo with vortioxetine 5 or 10 mg among patients who responded to open-label vortioxetine.

The primary endpoint was relapse within the first 24 weeks of double-blind treatment, defined by a MADRS score of 22 or more or investigator-assessed lack of efficacy. Relapse was reported in 26.0% of the placebo group and 13.2% of the vortioxetine group. The sponsor’s Cox-model analysis reported a hazard ratio of 2.01, with a 95% confidence interval from 1.26 to 3.21 and p = 0.004, for the listed comparison.

The result pertains to the analyzed responder population and the registered endpoint. Definitions of the FAS, missing-data methods, multiplicity procedures, and detailed statistical plan are not reported in the registry record. Secondary outcomes and adverse-event figures provide additional descriptive context but do not remove those limitations.