Safety, Efficacy and Tolerability of Vilazodone in (GAD) Generalized Anxiety Disorder: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety, Efficacy and Tolerability of Vilazodone in (GAD) Generalized Anxiety Disorder (NCT01844115), a randomized phase 3 study. The primary outcome is Change From Baseline in the Hamilton Rating Scale for Anxiety (HAM-A) Total Score.

2. Clinical Question

The study’s stated purpose was to evaluate the efficacy, safety, and tolerability of vilazodone relative to placebo in generalized anxiety disorder. The design used two parallel groups and a blinded comparison, allowing outcomes in the vilazodone arm to be considered alongside those in the placebo arm. Randomization is intended, in general, to make treatment groups comparable on average at the point of assignment; it does not guarantee that every characteristic is balanced, nor does the registry summary give details of the randomization procedure.

The primary endpoint concerns the average change in HAM-A total score from baseline to Week 8. The posted group means are 14.7 for placebo and 11.3 for vilazodone. The sponsor’s reported least squares mean difference is -2.20, with a 95% confidence interval from -3.72 to -0.68 and p = 0.005. The registry does not report a threshold for a clinically important difference, so the statistical contrast alone cannot establish how meaningful its size is to patients.

3. Trial Design

This was a Phase 3, randomized, triple-masked, parallel-group study comparing vilazodone with placebo in patients with generalized anxiety disorder. The official title describes a double-blind, placebo-controlled, flexible-dose study. The record lists Forest Laboratories as sponsor and the study status as completed. The recorded study start was 2013-04-30 and the primary completion date was 2014-03-31. Overall enrollment was 415.

The two interventions were oral vilazodone tablets and dose-matched oral placebo tablets. The trial’s stated purpose was to assess efficacy, safety, and tolerability relative to placebo. Although the record calls the vilazodone regimen flexible-dose, the actual dose levels, adjustment rules, and timing of dose changes are not reported in the registry record. The identities of the groups included in triple masking are also not specified.

The primary outcome was change from baseline in HAM-A total score, measured from baseline to Week 8. The primary outcome description defines the analysis population as the Intent-to-Treat population: patients in the Safety Population with at least 1 postbaseline HAM-A assessment. The outcome summaries list 200 participants in each group. These outcome-specific numbers should not be treated as a complete account of participant flow: the registry does not give a full breakdown of randomization, treatment received, missing assessments, or exclusions from each analysis.

The record also posts change from baseline in the Sheehan Disability Scale total score from baseline to Week 8 as a secondary outcome. The sponsor analyzed both posted outcomes using MMRM and reports least squares mean differences. The exact model specification, including the covariance structure, included covariates, and handling of intercurrent events, is not reported in the registry record. The registry does not report the original sample-size justification, a prespecified multiplicity strategy, or whether interim analyses were planned.

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: The Intent-to-Treat (ITT) Population consisted of all patients in the Safety Population who had at least 1 postbaseline assessment of the HAM-A.

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 Safety Population consisted of all patients in the Randomized Population who took at least 1 dose of double-blind investigational product.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in the Hamilton Rating Scale for Anxiety (HAM-A) Total Score, measured over Baseline to Week 8.

The primary endpoint is change from baseline to Week 8 in total score on the Hamilton Rating Scale for Anxiety, or HAM-A. The registry describes HAM-A as a clinician-administered scale made up of 14 items. Each item is rated on a five-point scale from 0 (not present) to 4 (very severe). The total can range from 0, described as absence of anxiety, to 56, described as the most severe form of anxiety.

A total score condenses ratings across the scale’s items into a single measure that can be compared between groups and over time. Measuring change from baseline is intended to focus the comparison on how the score shifts during the study rather than only on the score at one assessment. The Week 8 timeframe specifies the endpoint time used in the registry outcome description. The registry does not give further detail on the precise visit window or on how assessments outside the target visit were handled.

The HAM-A is used as a clinician-rated measure of anxiety symptom severity. Its scale description gives the interpretation of a score at an assessment, but the registry does not report a threshold for a clinically important change or the smallest difference considered meaningful. Thus, the numerical contrast and its uncertainty describe the measured group difference; they do not by themselves define the importance of that difference to patients.

The posted outcome is explicitly labeled as change from baseline, while the displayed group means are 14.7 for placebo and 11.3 for vilazodone. The registry does not spell out the sign convention used for these summaries. The sponsor’s reported comparison is a least squares mean difference of -2.20. Interpretation of the sign should therefore be tied to the endpoint coding and the model contrast as reported, rather than assuming an unreported convention.

7. Results Posted in the Registry

• Vilazodone: mean 11.30 versus 14.70 on control; difference -3.40 (95% CI -4.81 to -1.99), standardized effect d = -0.47; z-test p = <0.001.

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 in the Sheehan Disability Scale (SDS) Total 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 deviations.
• Result:
  • Vilazodone: mean 7.40 versus 9.20 on control; difference -1.80 (95% CI -3.16 to -0.44), standardized effect d = -0.26; z-test p = 0.010.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Vilazodone than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry posts one secondary outcome: change from baseline to Week 8 in Sheehan Disability Scale total score. The sponsor’s MMRM comparison and the unadjusted recalculation have the same general direction as the primary HAM-A results. This provides a related perspective because the secondary scale concerns disability, whereas HAM-A measures anxiety symptoms. The outcomes address distinct aspects of the study question and should not be treated as interchangeable measures.

Directional consistency across a symptom measure and a disability measure can add context to the pattern of results. It does not establish that one outcome confirms the other, and it does not resolve the limitations of the analyses or the uncertainty in the estimates. The registry does not report a clinically meaningful threshold for the SDS change, so the statistical contrast cannot be translated into a judgment about the importance of the disability difference.

The sponsor reports an MMRM analysis for this secondary endpoint, and a simple unadjusted comparison can also be calculated from the posted group summaries. As with the primary outcome, the sponsor’s model-based result and the unadjusted recalculation answer related but different statistical questions. The full model specification and missing-data details are not reported in the registry record.

Unadjusted secondary results carry less weight as confirmatory evidence when several outcomes or tests may have been considered. Testing multiple outcomes can increase the chance of at least one apparently notable result even if no corresponding effects exist. Statistical approaches such as prespecifying a hierarchy or adjusting significance thresholds can address that issue, but the registry does not report a multiplicity plan or adjustment. The secondary finding should therefore be interpreted as supportive context rather than treated as an independently definitive test. The record posts one secondary outcome, but it does not establish whether other outcomes were measured or considered in analyses beyond those posted.

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

• Change From Baseline in the Sheehan Disability Scale (SDS) Total Score

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports group means and standard deviations for continuous change scores, as well as a sponsor analysis using MMRM. These approaches answer related but not identical statistical questions. The group summaries describe the observed average change in each arm. A simple mean difference subtracts one arm’s mean from the other. The sponsor’s MMRM produces a model-based least squares mean difference, which can account for repeated measurements and other specified model terms. The registry does not report the complete model specification, so the exact adjustment and estimation details cannot be reconstructed from the record.

What does a mean difference describe?

A mean difference expresses the contrast between two group averages on the original outcome scale. For the primary comparison, the unadjusted value is -3.4 for vilazodone relative to placebo. Its sign reflects the subtraction order used in the comparison. A negative value means the vilazodone group’s posted mean is lower than the placebo group’s posted mean under that ordering. The clinical interpretation of lower change depends on the endpoint’s coding convention, which the registry does not spell out. The HAM-A description does establish that a lower score at an assessment corresponds to less severe anxiety, but a change-score sign needs to be read according to how change was coded.

Why is the sponsor’s estimate different?

MMRM means mixed model for repeated measures. In general, this type of model analyzes measurements collected over time while allowing observations from the same participant to be related. It can estimate group contrasts while using information across repeated assessments, subject to assumptions about the model and the observed data. A least squares mean is a model-based average, typically conditional on the terms included in the model. It need not equal the raw mean computed from the posted group summaries.

The sponsor’s primary result is a least squares mean difference of -2.20, whereas the simple unadjusted recalculation is -3.4. Their confidence intervals and p-values consequently differ as well. This is not evidence by itself that either calculation is erroneous: the two analyses use different information and methods. The sponsor’s own analysis takes precedence as the analysis reported for the trial. The record does not report enough details to assess the model’s chosen covariance structure, fixed effects, baseline adjustment, missing-data assumptions, or sensitivity analyses.

How should the confidence interval be read?

A confidence interval reflects estimation uncertainty under a particular analysis. In repeated use of the same method under its assumptions, intervals at a stated confidence level are designed to cover the underlying parameter at that rate. For an individual trial, the interval gives a range of values compatible with the data and method; it is not a guarantee that the true effect lies within the specific interval. A narrower interval indicates greater precision than a wider interval on the same scale. The primary sponsor interval is -3.72 to -0.68, and the unadjusted interval is -4.812 to -1.988; each belongs to its own analysis.

The interval’s relationship to zero helps describe whether the data are compatible with no difference under the analysis. An interval excluding zero is consistent with a nonzero contrast at the corresponding confidence level, given the model assumptions. It does not establish clinical relevance, eliminate the possibility of bias, or address whether multiple outcomes were tested. The sponsor reports p = 0.005 for the primary MMRM analysis; the simple recalculation reports p < 0.001. These p-values are not interchangeable because they derive from different analyses.

What does the unadjusted recalculation add?

The recalculated estimates are simple, unadjusted comparisons derived from posted summary statistics. They offer a transparent way to describe the difference between the listed group means and the uncertainty calculated for that comparison. They do not reproduce the sponsor’s MMRM and do not incorporate details that are unavailable in the registry record. The calculation assumes the posted summary data are suitable for that simple comparison; it does not resolve issues such as missing outcome observations, repeated-measure correlation, or any adjustment in the sponsor’s model.

The reported pooled standard deviation and standardized effect-size values provide scale-free descriptions of the contrast relative to outcome variability. Such standardized measures can help compare effects measured on different scales in general, but they do not provide a clinical threshold and do not substitute for the original score units. They also depend on the calculation and available summary statistics. No additional clinical interpretation should be assigned without a meaningful-change criterion.

Why can over-dispersion matter?

For count outcomes, over-dispersion means that observed variability exceeds what a simple statistical model assumes. It can make standard errors too small and confidence intervals too narrow if not addressed. That issue is not the central one for these continuous mean-change endpoints, which are reported with standard deviations. More generally, choosing a method that reflects the outcome’s distribution and dependence structure matters because uncertainty estimates depend on those assumptions. The registry identifies MMRM for the sponsor analyses but does not report diagnostic checks or alternative model choices.

Interpretation also depends on analysis populations and missing observations. The primary outcome population is described as patients in the Safety Population who had at least 1 postbaseline HAM-A assessment. MMRM can use available repeated outcome data under its modeling assumptions, but the registry record does not say how missing data were handled or whether those assumptions were evaluated. The available record therefore supports describing the reported estimates and their stated precision, but not a full audit of model validity.

11. Confidence Intervals and Precision

The primary sponsor estimate is a least squares mean difference of -2.20, with a 95% confidence interval from -3.72 to -0.68. The simple unadjusted recalculation is -3.4, with a 95% confidence interval from -4.812 to -1.988. These intervals quantify uncertainty for different estimands and methods; they should not be merged or treated as competing versions of one identical calculation. The sponsor interval reflects the reported MMRM analysis, while the recalculated interval comes from the posted group summaries.

Both primary intervals exclude zero. That indicates that zero is outside the ranges of values compatible with each analysis at the stated confidence level, subject to their respective assumptions. It does not make the point estimate exact. The sponsor interval allows for values between -3.72 and -0.68 under the model, while the recalculated interval spans -4.812 to -1.988 under the unadjusted method. The registry does not provide a threshold that would distinguish a clinically important difference from a smaller one, so precision on the score scale cannot by itself answer that question.

Confidence intervals are useful because they communicate both direction and uncertainty, unlike a p-value alone. A p-value summarizes how unusual the data would be under a specified null hypothesis and analysis; it does not describe the range of plausible effect sizes. The reported primary p-values are p = 0.005 for the sponsor’s analysis and p < 0.001 for the unadjusted recalculation. Their difference reflects the use of distinct statistical analyses and should not be read as a direct test of which analysis is preferable.

The interval widths also depend on the analysis population, variability, sample information, and modeling assumptions. The registry lists 200 participants in each primary outcome arm, but it does not give the time-specific number of observations used by the repeated-measures model or the missing-data pattern. Consequently, the posted confidence intervals describe the precision reported by the analyses, while the registry record does not support a detailed assessment of every source of uncertainty.

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 are planning calculations based on the observed effect, not a record of the trial’s original design justification. For these continuous outcomes, the listed figures are participants per arm, not total participants. The assumptions stated for the illustrations are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each scenario uses the stated fraction of the observed effect as the effect to detect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm in a hypothetical design that would have an 80% chance of detecting the specified effect under the illustration’s assumptions, if that effect were the true one. The 90% power column gives the corresponding planning number for a higher chance of detection. These are prospective planning quantities: they show what a design might require under the stated assumptions, not the probability that the completed trial found a real effect.

The rows consider planning for the full observed effect and for smaller fractions of that effect. As the effect to detect gets smaller, more participants are generally required to distinguish it from random variation with the same target power and significance level. The table and curve are therefore best read as sensitivity illustrations: they show how required enrollment changes when the target effect or desired power changes. Their values do not establish what effect was anticipated when the study was designed.

This is not observed power. Observed power, calculated after the trial from its estimated effect, is not a useful substitute for reading the effect estimate and confidence interval. The illustrations instead help with prospective planning, using the listed assumptions and observed effect as a reference point. They do not account for all possible design features, such as attrition or a particular repeated-measures analysis, unless those are included in the stated assumptions; no such additional assumptions are reported for these calculations.

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 = -3.400; pooled standard deviation σ = 7.203.
2. n = 2 × (1.96 + 0.842)² × 7.203² / -3.400² = 70.5, rounded up to 71 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 <- -3.4                      # observed difference in means
sigma <- 7.20306184896395                     # 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(1844115)
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 = 71 (80% power), 95 (90% power)
 75% of observed effect: n per arm = 126 (80% power), 168 (90% power)
 50% of observed effect: n per arm = 282 (80% power), 378 (90% power)
power.t.test: 71.4 
Simulated power at n = 71 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 sponsor’s primary analysis uses MMRM and reports a least squares mean difference of -2.20, a 95% confidence interval from -3.72 to -0.68, and p = 0.005. The recalculation from the posted group summaries gives an unadjusted mean difference of -3.4, a 95% confidence interval from -4.812 to -1.988, and p < 0.001. The estimates are not identical because the sponsor’s model-based analysis and the simple comparison of group means are different methods.

The recalculation is useful as a transparent check of the contrast implied by the posted means and standard deviations. It does not reproduce the sponsor’s repeated-measures model, account for model terms that may have been used, or replace the trial’s reported analysis. The registry does not give enough detail about the MMRM specification to explain the numerical difference fully. In particular, details such as the covariance structure, included covariates, and missing-data handling are not reported in the registry record.

There is no posted discrepancy flag for these results. Even so, the sponsor’s own analysis takes precedence when describing the trial’s prespecified or official analysis, because the recalculated result is only an unadjusted summary-statistic comparison. The two analyses both report intervals excluding zero, but neither result by itself establishes clinical importance. That interpretation would require a meaningful-change threshold or other clinical context, which is not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several hypotheses are tested. If each test is judged using its own nominal threshold without an adjustment or a prespecified testing sequence, the chance of at least one false-positive finding across the collection can be greater than for a single test. This matters when interpreting a primary endpoint together with secondary outcomes, especially if the results are used to make confirmatory claims.

The registry reports a primary HAM-A outcome and one posted secondary outcome, SDS total score. It gives sponsor MMRM p-values for both, as well as results that can be recalculated from the posted summaries. A multiplicity adjustment, testing hierarchy, or other strategy for controlling the overall error rate is not reported in the registry record. It is therefore not possible to determine from the registry whether the secondary outcome was intended as confirmatory, how its p-value should be judged in relation to the primary test, or whether additional planned comparisons were included in a broader testing family.

The record defines the primary outcome population as patients in the Safety Population who had at least 1 postbaseline HAM-A assessment. It does not provide a corresponding detailed analysis-population description for the secondary outcome. Overall enrollment was 415, and the posted outcome summaries list 200 participants per arm. The registry does not include a full participant flow or explain how many randomized participants lacked outcome observations, discontinued, or were excluded from a particular analysis.

Missing-data methods are particularly relevant to repeated measurements. MMRM can use available measurements under assumptions about the relationship between observed and unobserved values, but the validity of the resulting inference depends on those assumptions and model specification. The registry does not report the missing-data pattern, the model’s assumptions, imputation procedures, sensitivity analyses, or methods for handling treatment discontinuation and other intercurrent events. Those omissions limit independent assessment of robustness.

The registry also does not report whether interim analyses were planned or conducted, whether any stopping boundaries were used, or the original sample-size justification. No conclusion about these design and analysis features should be inferred from the posted endpoint results alone. The available information supports interpretation of the reported comparisons, but leaves important elements of the confirmatory analysis plan unresolved.

16. Safety Results

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

Deaths

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: laceration (0.5%), urinary tract infection, (0.5%), impaired gastric emptying (0.5%), stab wound (0.5%).

The registry lists serious adverse events for 202 participants at risk in each group. There were 0 serious adverse events in the placebo group and 3 in the vilazodone group. The listed top serious-event terms are Laceration, Urinary tract infection,, Impaired gastric emptying, and Stab wound, each recorded as 0.5%. The registry listing does not assign those individual terms to a treatment arm, so no arm-specific attribution should be inferred from that list.

For other adverse events, the record gives 81 affected participants among 202 at risk in the placebo group and 115 among 202 at risk in the vilazodone group. It reports 0 deaths in each group. Serious adverse events and other adverse events are separate categories in the registry reporting; the counts should not be combined or interpreted as if they described the same outcome definition.

These figures are descriptive counts. They do not by themselves establish a comparative safety profile, explain event severity beyond the serious-event classification, or show whether events were judged related to treatment. The registry does not provide further detail on event timing, duration, exposure-adjusted rates, or causality assessment. The numbers should therefore be read as the safety results posted for the recorded at-risk groups, with the limitations of the available detail.

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

The posted analyses describe a difference between the vilazodone and placebo groups in change from baseline on the primary HAM-A outcome through Week 8. The sponsor’s MMRM estimate is -2.20, with a 95% confidence interval from -3.72 to -0.68. The simple unadjusted estimate is -3.4, with a 95% confidence interval from -4.812 to -1.988. Both intervals exclude zero, but they come from different methods and should be interpreted according to their own assumptions.

These results do not, by themselves, establish how important the difference is to patients. The registry does not report a threshold for meaningful change on HAM-A, or information linking the score contrast to patient experience or functioning. It also does not state the sign convention for the displayed change summaries. The scale description explains that a lower HAM-A score at an assessment corresponds to less severe anxiety, but the interpretation of a change-score contrast depends on the coding used for change.

The result applies to the studied comparison and timeframe: vilazodone versus placebo in a Phase 3 randomized parallel-group study, with the primary outcome defined from baseline to Week 8. The record does not establish whether the same result would apply to other populations, regimens, follow-up periods, or comparators. The registry does not report enough design and analysis detail to assess every potential source of bias or uncertainty, including the missing-data assumptions and multiplicity strategy.

The secondary disability outcome shows a broadly similar direction in the sponsor analysis, but its interpretation is limited by the absence of a reported multiplicity plan and a clinical-change threshold. Safety counts are also available, including serious adverse events and deaths, but the registry summary does not provide sufficient detail to assess causality or event timing. Those data should be considered alongside, rather than substituted for, the primary outcome findings.

Statistical significance does not mean certainty, and a nonzero estimated difference does not alone show that the difference is large or consequential. The confidence intervals indicate a range of statistical uncertainty under the reported analyses, while the broader clinical meaning depends on context that is not reported in the registry record. The findings describe the posted evidence; they do not constitute medical advice or a recommendation about treatment.

18. Why This Trial Matters Statistically

This trial illustrates why readers should distinguish a raw comparison of group summaries from the sponsor’s model-based analysis. The posted means support a simple unadjusted contrast, while the sponsor reports an MMRM least squares mean difference. The estimates are related, but they are not identical quantities calculated by the same method. Reading both makes clear that model choice and analysis details matter when repeated measurements are involved.

It also demonstrates the value of reporting confidence intervals alongside p-values. The intervals communicate the range and precision of the estimated contrasts, while p-values address compatibility with a null hypothesis under an analysis. Neither measure answers the separate question of clinical importance. The registry does not report a meaningful-change threshold for either the HAM-A or SDS outcome, so that distinction is central to responsible interpretation.

The secondary endpoint emphasizes the role of multiplicity. A related disability measure can add context, but when several outcomes are analyzed, the interpretation of nominal p-values depends on whether a testing plan was specified. That plan is not reported in the registry record. This makes it important to distinguish a secondary finding that is descriptive or supportive from evidence intended to confirm a primary claim.

Finally, the record shows how incomplete reporting can constrain an otherwise straightforward reading. The primary analysis population is defined, and outcome group sizes and safety counts are posted, but the participant flow, MMRM specification, missing-data methods, original sample-size justification, and interim-analysis information are not reported. Statistical interpretation depends not only on estimates, but also on knowing how those estimates were produced and which uncertainties remain 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 complete participant flow from enrollment through randomization, treatment, follow-up, and analysis. Overall enrollment was 415, while the posted outcome summaries list 200 participants per arm. The primary population is defined, but the record does not explain the difference between total enrollment and the outcome-specific group counts or give a time-specific accounting of observations used in the repeated-measures model.

The sponsor’s MMRM is identified, but its full specification is not reported. Details of covariance structure, covariates, baseline adjustment, missing-data assumptions, sensitivity analyses, and handling of intercurrent events are unavailable in the record. These details would help readers assess how the modeled contrast was obtained and how robust it is to alternative assumptions. The unadjusted recalculation cannot fill that gap because it uses only the posted summary statistics.

The original sample-size justification and trial-specific design assumptions are not reported. The planning illustrations use the observed effect as a reference and cannot be taken as the design rationale for this study. The record also does not report whether interim analyses were planned or conducted, or any stopping rules.

A multiplicity strategy is not reported, limiting interpretation of the secondary outcome’s nominal statistical result. The registry does not provide thresholds for clinically meaningful change on HAM-A or SDS, and it does not spell out the sign convention for the posted change values. Accordingly, statistical contrasts can be described, but their patient-level importance is not established by the record.

For safety, the registry gives counts and selected serious-event terms but limited detail about timing, duration, treatment relatedness, or exposure. The serious-event term list is not broken down by group. These reporting limits constrain comparisons and do not support conclusions about causality from counts alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety, Efficacy and Tolerability of Vilazodone in (GAD) Generalized Anxiety Disorder — NCT01844115.
• Registry record last updated 2019-12-18; status last verified 2019-11.
• Results first posted 2019-12-18.
• 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 record describes a completed Phase 3, randomized, triple-masked, parallel-group study of oral vilazodone versus oral dose-matched placebo in generalized anxiety disorder. Forest Laboratories is listed as sponsor, and overall enrollment was 415. The primary outcome was change from baseline to Week 8 in HAM-A total score; the primary analysis population required at least 1 postbaseline assessment among patients in the Safety Population.

The sponsor reports an MMRM least squares mean difference of -2.20, with a 95% confidence interval from -3.72 to -0.68 and p = 0.005. The unadjusted recalculation from posted group summaries is -3.4, with a 95% confidence interval from -4.812 to -1.988 and p < 0.001. The posted secondary outcome concerns change in SDS total score. Serious adverse events were recorded in the group counts, and 0 deaths were reported in each arm.

The record does not report a clinical meaningful-change threshold, multiplicity strategy, full MMRM specification, original sample-size justification, or detailed missing-data methods. The results therefore describe the posted comparisons and their statistical precision, with those reporting limitations kept in view.