Study of the Safety and Effectiveness of JUVÉDERM VOLUX™ XC Injectable Gel for Restoring Jawline Definition: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of the Safety and Effectiveness of JUVÉDERM VOLUX™ XC Injectable Gel for Restoring Jawline Definition (NCT03712137), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Show ≥ 1-point Jawline Improvement on Both Sides From Baseline on the Allergan Loss of Jawline Definition Scale (ALJDS).

2. Clinical Question

The central statistical question is about the frequency of a defined response in each randomized group, and the uncertainty around the difference between those response frequencies. The endpoint is not a mean change in scale score: it classifies each participant according to whether the specified improvement threshold was met on both sides.

3. Trial Design

This was a phase 3, randomized, parallel-group controlled study of VOLUX XC for restoring jawline definition. The registry record describes the study as evaluator-blinded. It enrolled 206 participants and is marked completed. The study start date was 2018-11-12, and the primary completion date was 2020-02-04.

Participants were assigned to VOLUX XC or no-treatment control. The VOLUX XC arm received treatment on day 1, with an optional touch-up at day 30 and optional maintenance treatment at Month 12. The no-treatment group remained untreated during the control period, with optional delayed VOLUX XC treatment at the start of the post-control period. This means that the main comparison concerns the randomized treatment and control groups during the stated control period; later treatment options are also part of the study record.

The primary endpoint was assessed at Month 6. The registry describes the primary analysis population as modified intent-to-treat participants with a Month 6 ALJDS assessment on both sides of the jaw. Multiple imputation was used for participants missing that assessment. The primary outcome was reported as a responder percentage with a 95% confidence interval.

Other listed outcomes include investigator- and participant-assessed improvement using the Global Aesthetic Improvement Scale and change in the FACE-Q Satisfaction With Lower Face and Jawline Score. The registry record does not report the trial’s original sample-size assumptions, the detailed randomization procedure, or further details of masking beyond the evaluator-blinded description.

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.

Control Period

Opt VOLUX Treatment Follow Up Period

VOLUX Maintenance Treatment Period

Analysis population for the primary outcome, as defined in the registry: All modified intent-to-treat (mITT) participants who have Month 6 assessment on the ALJDS scale on both sides of the jaw. Multiple imputation was performed on participants with missing data for the Month 6 assessment on the ALJDS on both sides of jaw

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: Modified intent-to-treat (mITT) Population included all randomized participants with non-missing baseline on the ALJDS scale on both sides of the jaw

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Show ≥ 1-point Jawline Improvement on Both Sides From Baseline on the Allergan Loss of Jawline Definition Scale (ALJDS), measured over Month 6.

The primary endpoint asks whether participants achieved at least a 1-point improvement from baseline on both sides of the jaw at Month 6. The assessment used the Allergan Loss of Jawline Definition Scale, an investigator assessment of loss of jawline definition on a 5-point scale ranging from 0, None, to 4, Extreme. The endpoint turns that scale assessment into a responder classification: a participant either met the specified improvement criterion on both sides or did not.

A responder percentage is useful because it expresses how often a prespecified level of change was observed, rather than describing only an average score. Requiring improvement on both sides makes the criterion explicit. The endpoint does not, by itself, describe the size of improvement beyond the threshold or the distribution of scale changes among participants who did not meet it.

The primary time point was Month 6. The registry record specifies an analysis population comprising modified intent-to-treat participants with assessments on both sides of the jaw, and says multiple imputation was used for missing Month 6 assessments. As with any binary endpoint, interpretation depends on the response definition, the assessment process, the handling of missing data, and the precision of the estimated percentages and group contrast.

7. Results Posted in the Registry

• VOLUX XC: 68.8% (108/157) versus 38.8% (19/49) on control; risk difference 30.0 percentage points (95% CI 14.6 to 45.5), risk ratio 1.77 (1.23–2.56); unadjusted two-proportion 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.

Percentage of Participants Who Note "Improved" or "Much Improved" in Jawline Area as Assessed by the Evaluating Investigator Using the Global Aesthetic Improvement Scale (GAIS)

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • VOLUX XC: 89.0% (130/146) versus 28.9% (13/45) on control; risk difference 60.2 percentage points (95% CI 46.0 to 74.3), risk ratio 3.08 (1.94–4.89); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for VOLUX XC than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes listed in the registry address related but distinct questions: investigator-assessed and participant-assessed global improvement, and change in satisfaction with the lower face and jawline. These measures can complement the ALJDS responder endpoint because they reflect different assessments or a different construct. They are not interchangeable with the primary endpoint, which uses a specific scale-based improvement threshold on both sides of the jaw.

Posted results are available for the investigator-assessed GAIS outcome at Month 6. The observed pattern is consistent in direction with the primary result: the posted investigator assessment reports more participants classified as improved or much improved in the VOLUX XC group than in the control group. Results for participant-assessed GAIS and FACE-Q change are not reported in the registry record. The record also contains no reported sponsor analysis for the posted investigator-assessed secondary outcome.

Secondary findings generally carry less weight than the primary endpoint when the registry record does not report a multiplicity strategy. Testing several outcomes can increase the chance that at least one result appears statistically persuasive by chance. The full prespecification and multiplicity plan are not reported in the registry record, so the secondary results should be viewed as supportive descriptive evidence rather than treated as independent confirmation of the primary finding.

The endpoints also differ in who makes the assessment and what is measured. The investigator-rated GAIS is not the same as participant-rated improvement or a satisfaction score. Without posted results for all listed secondary outcomes, the record does not support a complete comparison of the pattern across every measure. The available secondary result aligns directionally with the primary result, but it does not resolve these missing pieces or replace the primary analysis.

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

• Percentage of Participants Who Note "Improved" or "Much Improved" in Jawline Area as Assessed by the Evaluating Investigator Using the Global Aesthetic Improvement Scale (GAIS)
• Percentage of Participants Who Note "Improved" or "Much Improved" in Jawline Area as Assessed by the Participant Using the Global Aesthetic Improvement Scale (GAIS)
• Change From Baseline in Overall Score for FACE-Q™ Satisfaction With Lower Face and Jawline Score

9. Statistical Interpretation

10. Statistical Methods Explained

What does a responder percentage represent?

A binary responder endpoint sorts participants into two categories according to a stated rule. In this trial, the rule was at least a 1-point improvement from baseline on both sides of the jaw at Month 6. The reported percentage is the proportion classified as responders within the relevant analysis group. It does not show how far each responder improved beyond the threshold, nor does it preserve all the information in the original scale.

Binary endpoints can be easy to interpret in terms of how many participants met a criterion. Their interpretation depends strongly on the chosen threshold and assessment procedure. Participants just below and just above a threshold may have similar scale results but fall into different categories. The scale description and responder rule therefore matter when reading the group percentages.

What is a risk difference?

A risk difference compares the responder proportions in two groups by subtracting one group’s proportion from the other’s. The recalculated estimate is 0.300, with a 95% confidence interval from 0.146 to 0.455. Its positive direction reflects the higher observed responder percentage in the VOLUX XC arm. This recalculation is unadjusted and is based on the posted group summary statistics; it is distinct from the sponsor’s reported analysis.

Risk differences keep the comparison on an absolute scale: they describe the gap between the two response proportions. Other relative measures can express the same comparison differently, but the registry’s sponsor analysis reports a responder rate difference. A measure’s scale affects how easily readers can relate it to the observed proportions; no single measure replaces the need to inspect the underlying group results and their uncertainty.

What does a confidence interval express?

A confidence interval is a measure of statistical precision around an estimate. In general, a 95% confidence interval is produced by a method that, under its assumptions and repeated use, would cover the underlying parameter in 95% of such intervals. It is not a statement that there is a 95% probability that the particular fixed parameter lies inside the interval. The interval’s width reflects uncertainty from the data and method; it does not capture every source of uncertainty, such as limitations in study conduct or outcome measurement.

For the contrast, the recalculated interval extends from 0.146 to 0.455. For the group percentages, the posted intervals are 61.53 to 76.39 for VOLUX XC and 24.25 to 51.8 for no-treatment control. The sponsor’s imputation-based interval for the responder rate difference extends from 15.33 to 46.54. Each interval pertains to its own estimate and analysis method; the endpoints should not be conflated.

Why does missing-data handling matter?

The primary analysis population is described as modified intent-to-treat participants with Month 6 assessments on both sides of the jaw. The record states that multiple imputation was performed for missing Month 6 assessments. Multiple imputation is a general statistical approach that uses a model to represent uncertainty about missing values, creating multiple completed datasets and combining analyses across them. Its validity depends on the model and assumptions about why data are missing and how missingness relates to observed information.

The registry record does not report the imputation model, the variables included, the number of imputed values, or sensitivity analyses examining alternative assumptions. Consequently, readers can identify that imputation was used but cannot fully assess its implementation or how robust the result is to different missing-data assumptions.

Why can over-dispersion matter?

Over-dispersion is a general issue in models for counts or proportions when observed variability is greater than the model’s assumed variability. It can lead to standard errors that are too small if not addressed, making intervals appear too narrow and statistical evidence appear stronger than warranted. The primary endpoint is reported as a binary responder percentage, but the registry record does not describe a model-based analysis that would establish whether over-dispersion was relevant or how it was handled. It should not be assumed to have occurred.

What does the p-value add?

A p-value measures how incompatible the observed data are with a specified null model, under the assumptions of the analysis. The recalculation reports p < 0.001, while the sponsor’s analysis reports p < 0.001. A p-value is not the probability that the null hypothesis is true, and it does not quantify the size or practical importance of an effect. The estimates and confidence intervals remain important because they describe the direction, magnitude on the reported scale, and precision of the contrast.

The record identifies the sponsor analysis as a superiority analysis. The detailed statistical analysis plan, including any adjustment details beyond the stated multiple imputation, is not reported in the registry record. Therefore, the p-values should be read as results of the analyses as reported, not as evidence that every analytic choice or assumption can be independently evaluated from the record.

11. Confidence Intervals and Precision

Precision is conveyed by the confidence intervals around the responder percentages and the group contrast. For the primary Month 6 result, the VOLUX XC estimate is 69, with a 95% confidence interval from 61.53 to 76.39. The no-treatment estimate is 38, with a 95% confidence interval from 24.25 to 51.8. These intervals show that the estimated response frequencies have uncertainty, and the width differs between the groups.

The unadjusted recalculated risk difference is 0.300, with a 95% confidence interval from 0.146 to 0.455. This interval is for the contrast, not for either arm’s response percentage. It spans positive values, consistent with the observed direction of the group difference. The sponsor’s multiple-imputation analysis reports a responder rate difference of 30.9, with a 95% confidence interval from 15.33 to 46.54. That interval belongs to the sponsor’s analysis and should be read separately from the recalculated interval.

Confidence intervals describe sampling uncertainty under the methods and assumptions used. They do not account automatically for every limitation, including possible measurement issues, unreported analysis choices, or assumptions about missing data. The registry record identifies multiple imputation for missing Month 6 assessments but does not report enough detail to evaluate all imputation assumptions.

Precision also depends on the analysis population and endpoint definition. The primary results use participants in the stated modified intent-to-treat population, with imputation for missing assessments. The interval does not imply that a particular individual’s response can be predicted from the group-level estimate. It summarizes uncertainty in a population-level statistic, not individual variability or the certainty of an individual outcome.

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 figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses a stated fraction of the observed effect as the effect to detect. The figures are participants per arm for 80% power and participants per arm for 90% power, not total events.

The 80% power column gives the planned number of participants in each arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the assumptions were correct. The 90% power column uses a higher target probability of detection and therefore generally requires more participants per arm. The displayed scenarios consider planning for 100%, 75%, and 50% of the observed effect.

Smaller effects are harder to distinguish from random variation, so planning for a smaller effect requires more participants per arm. The table and curve help illustrate this relationship; they do not recover the rationale for the trial’s actual enrollment. The trial’s original sample-size justification and design assumptions are not reported in the registry record.

These figures are planning illustrations, not observed power. Observed power is not a useful substitute for reading the estimated effect and its confidence interval; the illustration instead shows how sample-size requirements change under specified hypothetical planning assumptions.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.388; treatment proportion p₁ = 0.688; average p̄ = 0.538.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7051 = 1.3819.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6724 = 0.5659.
4. n = (1.3819 + 0.5659)² / (0.3001)² = 42.1, rounded up to 43 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
p0 <- 0.387755102040816                          # control proportion
p1 <- 0.687898089171974                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3712137)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 43 (80% power), 56 (90% power)
 75% of observed effect: n per arm = 77 (80% power), 102 (90% power)
 50% of observed effect: n per arm = 173 (80% power), 230 (90% power)
power.prop.test: 42.1 
Simulated power at n = 43 per arm: 0.806 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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 reports a sponsor analysis using multiple imputation, with a responder rate difference of 30.9, a 95% confidence interval from 15.33 to 46.54, and p < 0.001. The analysis is identified as a superiority analysis. Its result is the sponsor’s reported analysis of the primary endpoint and takes precedence over the unadjusted recalculation when interpreting the sponsor’s analysis.

The recalculated risk difference is 0.300, with a 95% confidence interval from 0.146 to 0.455 and p < 0.001. It is a simple unadjusted recalculation from posted summary statistics, not a reconstruction of the sponsor’s multiple-imputation procedure. The two estimates are expressed on different displayed scales and arise from analyses with different stated handling of missing data. They should not be treated as interchangeable.

The discrepancy indicator is false, and the results have a broadly consistent direction: both analyses report a positive responder difference favoring the VOLUX XC group. The registry record does not report the full statistical analysis plan or enough detail to reproduce the sponsor’s imputation analysis. Interpretation of the sponsor result therefore rests on the reported estimate and interval, alongside the analysis description available in the record.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when an analysis evaluates more than one outcome, time point, group contrast, or other hypothesis. If each is tested without an adjustment or a prespecified hierarchy, the chance of at least one false-positive finding can increase. This is a general statistical concern, not evidence that a particular reported result is false. The registry lists multiple secondary outcomes, but the multiplicity strategy and detailed testing hierarchy are not reported in the registry record.

The primary endpoint is identified, and the sponsor’s analysis is marked as a superiority analysis. The registry does not report the full statistical analysis plan, including whether or how the primary inference was protected against other planned analyses. The secondary outcomes should therefore be interpreted with appropriate caution, especially where no sponsor analysis is posted. The registry record also does not report interim analyses or stopping rules; their use or non-use should not be inferred.

Missing data are relevant to the primary endpoint. The stated population includes modified intent-to-treat participants with Month 6 assessments on both sides of the jaw, and multiple imputation was performed for missing Month 6 assessments. Multiple imputation is designed to reflect uncertainty about missing values, but its performance depends on the imputation model and assumptions. The model details, missingness reasons, amount of missing data, and sensitivity analyses are not reported in the registry record.

The record does not provide enough information to judge whether missingness could have depended on unobserved outcomes or whether alternative assumptions would change the result. The sponsor estimate and the recalculation also have different stated approaches: the sponsor analysis uses multiple imputation, whereas the recalculation is unadjusted from the posted summary statistics. This distinction matters when comparing the estimates.

The primary analysis population is described, but further details about analysis populations for all endpoints are not reported in the registry record. The randomized design is stated; the registry does not give additional detail about allocation concealment or the precise implementation of masking. These omissions limit assessment of the full analysis process without establishing that any particular method was inadequate.

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: injection site nodule (2.4%), bacterial vaginosis (2.4%), covid-19 (2.4%), clostridium difficile infection (2.4%), diverticulitis (2.4%).

The registry reports serious adverse events and other adverse events for several treatment-period groups. In the initial no-treatment control group, 1 serious adverse event was reported among 50 participants at risk, and 0 other adverse events were reported; there were 0 deaths. In the VOLUX XC treatment group, 17 serious adverse events and 9 other adverse events were reported among 156 participants at risk; there were 0 deaths.

Separate post-control and maintenance treatment groups are also listed. The optional VOLUX XC post-control group had 3 serious and 5 other adverse events among 42 participants at risk, with 0 deaths. The VOLUX maintenance group had 4 serious and 1 other adverse event among 87 participants at risk, with 0 deaths. These groups represent different treatment periods and should not be assumed to be parallel randomized comparison groups.

The serious-event terms listed most often include INJECTION SITE NODULE, BACTERIAL VAGINOSIS, COVID-19, CLOSTRIDIUM DIFFICILE INFECTION, DIVERTICULITIS, and SINUSITIS, with the percentages reported in the registry. These are event terms, not causal conclusions. The adverse-event figures alone do not establish whether an event was caused by treatment or permit a complete benefit-risk assessment. The registry record does not report further detail on event timing, severity beyond seriousness, or attribution.

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

The primary result describes how often participants met a defined Month 6 improvement criterion in each study group. The reported responder percentage was higher in the VOLUX XC arm than in no-treatment control, and the recalculated group contrast and sponsor-reported analysis both point in the same direction. Their confidence intervals communicate uncertainty around the respective estimates.

This result does not mean that every participant in the VOLUX XC group met the response criterion, or that no participant in the control group did. It does not describe each person’s experience, the amount of change beyond the threshold, or the persistence of any individual response. It is a group-level finding tied to the ALJDS assessment at Month 6 and the stated analysis population.

The endpoint is one measure of jawline change. The listed secondary outcomes include global improvement ratings and satisfaction, but the registry record does not report results for all of them. Nor does the primary result resolve how different outcome definitions, missing-data assumptions, or analysis choices might affect estimates. Multiple imputation was used for missing Month 6 primary assessments, but the imputation details and sensitivity analyses are not reported in the registry record.

Statistical separation between groups is not, by itself, a judgment about clinical importance. The registry record does not provide a threshold for interpreting the size of the group difference as clinically meaningful. The results also do not establish how well they generalize beyond the study population or circumstances described in the record. No medical advice or treatment recommendation follows from these statistics alone.

18. Why This Trial Matters Statistically

This trial illustrates how a clinical question can be expressed as a binary responder endpoint and a comparison of responder frequencies between randomized groups. The primary outcome defines improvement in advance as at least a 1-point change from baseline on both sides of the jaw. That rule makes the response criterion interpretable, while also making the result dependent on the selected threshold and assessment scale.

The reported group percentages and confidence intervals show why effect estimates should be read alongside tests of statistical significance. A p-value addresses compatibility with a null model under analysis assumptions; it does not convey the full size or precision of a group contrast. The recalculated risk difference and the sponsor’s imputation-based responder rate difference also demonstrate why analysis methods and scales must be identified before estimates are compared.

The record highlights the importance of missing-data handling: multiple imputation was used for the primary endpoint, while details needed to assess that approach are not reported. It also provides a useful example of how secondary outcomes may broaden the clinical picture while raising multiplicity and completeness questions. Some listed secondary results are not reported in the registry record, and no multiplicity strategy is described.

Finally, the safety record separates treatment periods and groups, including optional post-control and maintenance treatment. Those figures require attention to denominators and study phases rather than being read as a single simple comparison. Together, these features show why transparent reporting of endpoint definitions, analysis populations, missing-data methods, and uncertainty is essential to a careful statistical reading of a trial.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record does not report the original sample-size justification or the assumptions used to plan enrollment. The planning illustrations based on the observed effect cannot substitute for those design details. The record also does not give the full statistical analysis plan, the exact randomization procedures, or further detail about masking beyond the evaluator-blinded description.

The primary result depends on a binary responder definition using a 1-point improvement on both sides. That classification does not retain the full scale information and does not describe the amount of improvement for each participant. Results are reported at Month 6; the primary endpoint therefore does not establish a pattern at other time points.

Multiple imputation was used for missing primary assessments, but the imputation model, missingness reasons, quantity of missing data, and sensitivity analyses are not reported in the registry record. This limits independent assessment of the missing-data assumptions. The sponsor estimate and unadjusted recalculation also differ in analysis approach, so the recalculation should not be treated as a reproduction of the sponsor’s analysis.

The registry lists several secondary outcomes, but results are not reported for participant-assessed GAIS or FACE-Q change. A multiplicity plan is not reported, which limits the strength of conclusions drawn from secondary findings. The adverse-event information gives counts for multiple treatment periods, but does not provide all details needed to assess event timing, attribution, or the relationship between individual participants’ exposures and outcomes. These reporting limitations do not by themselves show that the study methods were deficient; they identify what cannot be assessed from the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of the Safety and Effectiveness of JUVÉDERM VOLUX™ XC Injectable Gel for Restoring Jawline Definition — NCT03712137.
• Registry record last updated 2023-01-04; status last verified 2022-09.
• Results first posted 2023-01-04.
• 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

NCT03712137 is a completed phase 3 randomized, parallel-group study of VOLUX XC compared with no-treatment control for restoring jawline definition. The registry describes the study as evaluator-blinded and reports enrollment of 206 participants.

The primary endpoint was the percentage of participants with at least a 1-point ALJDS improvement on both sides of the jaw at Month 6. The posted results report higher response in the VOLUX XC group than in no-treatment control. The sponsor’s reported analysis used multiple imputation and included a 95% confidence interval; an unadjusted recalculation is also available and should be understood as a distinct analysis.

Secondary outcomes include investigator- and participant-assessed GAIS improvement and FACE-Q satisfaction change. Not all listed secondary results are reported in the registry record. The record also includes serious and other adverse-event counts across initial, post-control, and maintenance treatment groups. Details of the original sample-size assumptions, full analysis plan, multiplicity strategy, and imputation model are not reported.