Evaluation of the Effectiveness and Safety of the Ulthera® DeepSEE® System for Treating Skin Laxity in the Lower Face and Submentum: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of the Effectiveness and Safety of the Ulthera® DeepSEE® System for Treating Skin Laxity in the Lower Face and Submentum (NCT04795622), a randomized na study. The primary outcome is Percentage of Subjects With Improvement in Lower Face and Submental Skin Laxity at Day 90.

2. Clinical Question

3. Trial Design

This was a randomized, single-masked, parallel-group trial of the Ulthera DeepSEE System for skin laxity in the lower face and submentum. The registry lists an enrollment of 201 and a completed study. It records a start date of 2021-03-16 and a primary completion date of 2022-01-18. The phase is listed as not applicable.

Participants were allocated to treatment with the Ulthera DeepSEE System or to untreated control with delayed treatment. The registry identifies the study as single-masked but does not state which participants or study personnel were masked. It also does not report further details of the randomization procedure or allocation concealment.

The primary endpoint was assessed at Day 90 using photographs taken at baseline and Day 90. Three blinded evaluators compared the photographs, and improvement required agreement from at least two evaluators. The primary analysis population was the full analysis set, defined as all randomized participants with baseline photographs of acceptable quality. The arm counts for the posted primary outcome are 96 in the treatment group and 100 in the untreated-control group.

The registry describes the study objectives as demonstrating superiority to untreated control for improvement in skin laxity and assessing safety. It lists secondary outcomes covering submental skin displacement, investigator- and participant-rated aesthetic improvement, FACE-Q satisfaction with the lower face and jawline, and treatment-related treatment-emergent adverse events. Original design assumptions, including the trial’s own sample-size justification, are not reported in the registry record.

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: Of the 213 screened subjects,12 were exited as screen failures and 201 subjects were enrolled and randomized in this study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The full analysis set (FAS) included all subjects randomized with baseline photographs of acceptable quality.

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: SES included all subjects who were treated.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Subjects With Improvement in Lower Face and Submental Skin Laxity at Day 90, measured over Day 90.

The primary endpoint is the percentage of participants with improvement in lower-face and submental skin laxity at Day 90. Improvement was assessed by comparing baseline photographs with Day 90 photographs. Three blinded evaluators made the assessments, and the endpoint counted a participant as improved when at least two evaluators judged the later photographs improved relative to baseline.

This is a binary participant-level outcome: each participant is classified as improved or not improved according to the stated evaluator rule. Reporting the percentage makes the comparison interpretable as the proportion of participants meeting that definition in each group. It does not measure the size of an individual participant’s change in laxity.

Photographic assessment with blinded evaluators offers a defined way to compare appearance over time while limiting the influence of knowledge of treatment on the evaluators’ judgments. Requiring agreement among at least two evaluators sets a prespecified-seeming decision rule in the endpoint description, but whether and when that rule was finalized is not reported in the registry record. Nor does the endpoint description establish that the assessment captures every aspect of skin laxity or participants’ experience. Other outcomes in the registry address different measures, including participant satisfaction and aesthetic improvement.

7. Results Posted in the Registry

• Treatment With Ulthera DeepSEE System: 54.2% (52/96) versus 47.0% (47/100) on control; risk difference 7.2 percentage points (95% CI -6.8 to 21.1), risk ratio 1.15 (0.87–1.52); unadjusted two-proportion z-test p = 0.316.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary because each participant either met the endpoint definition of improvement or did not. For a binary outcome, a group percentage estimates the proportion of participants with the event of interest. The registry reports 54.2% for treatment and 47.0% for untreated control. Those percentages describe the observed groups; they are not estimates free of sampling uncertainty.

What does the risk difference express?

The recalculated unadjusted risk difference is 0.072, with treatment compared against untreated control. A risk difference expresses the contrast between two proportions on an absolute scale. Its no-difference value is zero. The confidence interval, from -0.068 to 0.211, spans that value, so the posted estimate does not rule out no difference under this analysis. The interval also extends to values in either direction, illustrating why the point estimate alone does not describe the precision of the comparison.

What does an odds ratio express?

An odds ratio compares the odds of meeting the endpoint in one group with the odds in the other. The registry’s sponsor analysis reports an odds ratio, while the recalculation also presents an odds ratio of 1.333 with a confidence interval from 0.76 to 2.337. The ratio’s no-association value is one. A confidence interval that crosses this value includes the possibility of no association on the odds-ratio scale. Odds and probabilities are distinct quantities, so the odds ratio should not be read as a direct percentage-point change or as a risk ratio.

The recalculated risk ratio is 1.152, with a confidence interval from 0.873 to 1.522. A risk ratio compares the two group probabilities directly as a ratio. Its no-difference value is one. It is another way to express the same binary-outcome comparison, not a separate endpoint. The three measures—risk difference, risk ratio, and odds ratio—use different scales and answer related but non-identical descriptive questions.

What does the p-value say?

The recalculated unadjusted p-value is 0.316. In general, a p-value describes how compatible the observed data are with a specified null model, assuming the model and test assumptions apply. It is not the probability that the null hypothesis is true, nor is it a measure of clinical importance. The registry’s sponsor analysis does not include a p-value, and its analysis method is not reported in the registry record.

These recalculations are unadjusted comparisons based on posted group summaries. They do not incorporate covariate adjustment or other modeling unless that is explicitly stated; adjusted analyses are not described in the registry record. The recalculated estimates are therefore useful descriptive comparisons, but they do not replace the sponsor’s own analysis. The registry’s reported odds ratio and the recalculated estimates may use different methods or analysis details, which are not fully specified in the record.

Why does over-dispersion matter?

General statistical context: for binary outcomes, variability can differ from what a simple model assumes when observations are more heterogeneous than that model allows. This is often called over-dispersion. If it is present and ignored, standard errors and confidence intervals may not reflect the actual variability. The registry record does not report an over-dispersion assessment or a model that accounts for it, and no conclusion about its presence can be drawn from the posted summaries alone.

The primary endpoint depends on judgments from blinded evaluators. General statistical context: an outcome based on multiple assessments requires a clear rule for combining those assessments; agreement thresholds help define the final classification. The registry specifies that at least two of three evaluators must assess the photographs as improved. It does not report evaluator agreement statistics, details of adjudication, or procedures for handling an unavailable or ungradable photograph.

10. Confidence Intervals and Precision

The recalculated risk difference is 0.072, and its confidence interval runs from -0.068 to 0.211. This interval is wide enough to include no difference and to include estimates in either direction. It therefore indicates limited precision about the size and direction of the underlying contrast, despite the point estimate being positive. The range is an uncertainty interval for the estimated comparison, not a range containing a known proportion of individual participant outcomes.

The recalculated risk-ratio interval, from 0.873 to 1.522, also includes its no-difference value. The recalculated odds-ratio interval, from 0.76 to 2.337, likewise includes its no-association value. These intervals express uncertainty on different scales. Neither should be interpreted as a probability statement about the true effect.

General statistical context: a confidence interval is constructed by a method intended to capture the underlying parameter at its stated confidence level over repeated use of that method, when its assumptions hold. A wider interval generally means less precision. The registry’s sponsor analysis reports a 95% confidence interval for its odds ratio; its numerical limits are reported separately in the sponsor reading. The recalculated intervals are not labeled with a confidence level in the posted recalculation details, so a level should not be inferred for them.

Precision is influenced by the number of analyzed participants, the frequency of the outcome, and the analysis method. The primary population requires acceptable-quality baseline photographs, and the primary outcome is based on evaluator judgments. The registry does not report the number or handling of participants excluded from the full analysis set, missing Day 90 photographs, or ungradable assessments. Those omissions limit assessment of whether the displayed intervals capture all relevant uncertainty.

11. 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 planning figures are participants per arm, not total events. They are illustrations based on the observed effect rather than the trial’s original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is a stated fraction of the observed effect.

For planning at 100% of the observed effect, the illustration gives 763 participants per arm for 80% power and 1,021 participants per arm for 90% power. At 75% of the observed effect, the corresponding figures are 1,358 and 1,817 participants per arm. At 50% of the observed effect, they are 3,054 and 4,088 participants per arm.

In general, power is the chance that a planned study will detect an effect of a specified size under its assumptions, if that effect is present. The 80% power column gives the participants per arm indicated by the planning calculation for an 80% chance of detecting the chosen effect; the 90% column gives the count for a 90% chance. The higher power target requires more participants under these assumptions. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm as the target effect gets smaller.

These are planning illustrations, not observed power and not evidence that the trial was designed to these assumptions. The trial’s own design assumptions and sample-size justification are not reported in the registry record. The figures also depend on the calculation’s stated assumptions and should not be treated as a prediction of the trial’s actual results.

12. 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 = 0.470; treatment proportion p₁ = 0.542; average p̄ = 0.506.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7071 = 1.3858.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7052 = 0.5935.
4. n = (1.3858 + 0.5935)² / (0.0717)² = 762.8, rounded up to 763 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 <- 0.47                          # control proportion
p1 <- 0.541666666666667                          # 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(4795622)
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 = 763 (80% power), 1,021 (90% power)
 75% of observed effect: n per arm = 1,358 (80% power), 1,817 (90% power)
 50% of observed effect: n per arm = 3,054 (80% power), 4,088 (90% power)
power.prop.test: 762.8 
Simulated power at n = 763 per arm: 0.798 (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.

13. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparison as an odds ratio of 1.355 with a 95% confidence interval from 0.753 to 2.437. That interval crosses the odds-ratio value corresponding to no association. A p-value for the sponsor analysis is not reported in the registry record, and the method used for that analysis is also not reported in the registry record.

The recalculation from the posted group summaries gives an odds ratio of 1.333, with a confidence interval from 0.76 to 2.337. It also gives an unadjusted risk difference of 0.072, with a confidence interval from -0.068 to 0.211, and an unadjusted p-value of 0.316. These are simple unadjusted recalculations and may not reproduce every detail of the sponsor’s analysis method.

The sponsor’s own analysis takes precedence over the recalculation when describing the sponsor-reported result. Both the sponsor’s confidence interval and the recalculated intervals include their respective no-difference values. The estimates are close in direction, but the measures and potentially the analysis details differ, so they should not be treated as exact duplicates.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists the primary Day 90 improvement outcome and five secondary outcomes. The secondary outcomes address submental skin displacement, investigator-rated and participant-rated aesthetic improvement, FACE-Q satisfaction with the lower face and jawline, and treatment-related treatment-emergent adverse events. Quantitative results for these secondary outcomes are not reported in the registry record.

Multiplicity arises when several outcomes or comparisons are tested. In general, conducting many tests can increase the chance of at least one apparently notable result by chance. Statistical plans may address this through a prespecified testing hierarchy or an adjustment procedure. Whether this trial used such an approach, and whether any secondary outcomes were designated for confirmatory testing, are not reported in the registry record. The available material therefore does not support an assessment of multiplicity control.

The primary endpoint population is the full analysis set, defined as randomized participants with baseline photographs of acceptable quality. The registry does not report the number of randomized participants excluded from this set, reasons for exclusion, or the handling of missing Day 90 photographs and other missing outcomes. It also does not report whether any imputation or sensitivity analysis was used. These details matter because missingness or exclusions can affect both the analyzed population and the interpretation of the estimated treatment contrast.

The registry reports four analyses, but the full statistical analysis plan is not reported in the registry record. The method for the sponsor’s odds-ratio analysis is also not reported. There is no reported description of interim analyses, covariate adjustment, protocol deviations, or prespecified subgroup analyses. Their absence from the registry record should not be taken as evidence that they were or were not conducted.

15. 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: cholelithiasis (1.0%), fractured sacrum (1.0%), radius fracture (1.0%), gastric leiomyoma (1.0%).

For serious adverse events, the registry lists 3 affected participants among 97 at risk in the treatment group and 0 among 96 at risk in the untreated-control/delayed-treatment group. The registry lists zero deaths in both groups. These counts describe the recorded events in the groups and do not establish that an event was caused by treatment.

The listed serious-event terms are cholelithiasis, fractured sacrum, radius fracture, and gastric leiomyoma; each is recorded as 1.0%. The registry does not provide further detail on event timing, severity beyond the serious-event classification, outcomes, or causal assessment for each term. The reported term percentages should be read as posted, rather than used to infer unreported denominators or individual-level patterns.

The registry also lists other adverse events affecting 34 participants among 97 at risk in the treatment group and 32 among 96 at risk in the untreated-control/delayed-treatment group. Those figures are distinct from serious adverse events. The outcome list includes treatment-related treatment-emergent adverse events, but the posted aggregate figures do not by themselves identify which events were considered related to treatment. Safety interpretation is therefore limited to the recorded counts and the event categories described.

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

The primary result describes the proportion of participants classified as improved by the specified photographic assessment at Day 90. The observed percentages were 54.2% with treatment and 47.0% with untreated control. The unadjusted risk-difference estimate was 0.072, but its confidence interval, from -0.068 to 0.211, includes no difference. The unadjusted p-value was 0.316. These statistics show uncertainty about the size and direction of the underlying difference.

The result does not establish that the groups differ, nor does it prove that they are equivalent. A confidence interval that includes no difference can arise when the estimate is imprecise; it does not show that the true difference is exactly zero. The available analysis also does not establish the clinical importance of any particular difference. The registry record does not state a threshold for a meaningful improvement or a minimum important between-group difference.

The endpoint is specific to blinded evaluators’ judgments of baseline and Day 90 photographs. It does not directly quantify the magnitude of laxity change, and it is distinct from participant satisfaction or other aesthetic outcomes. Quantitative results for the listed secondary outcomes are not reported in the registry record. The primary finding should not be generalized to those separate measures.

The findings are limited to the analyzed population and the stated assessment time. They do not describe outcomes beyond Day 90 or establish how the result would apply to populations not represented in the trial. The available safety counts likewise describe recorded events; they do not prove or exclude a causal relationship between treatment and any individual event.

Overall, the posted data provide an estimate and its uncertainty for a defined comparison and outcome. They are not, by themselves, a complete account of the trial’s analysis plan, missing data, multiplicity, or all safety details. Those aspects are not reported in the registry record.

17. Why This Trial Matters Statistically

This trial is statistically informative because its primary outcome uses a clearly described binary rule: improvement is counted when at least two of three blinded evaluators judge Day 90 photographs improved relative to baseline. That definition makes the endpoint and its group percentages interpretable, while also highlighting that the result depends on categorical judgments rather than a direct continuous measure of change.

The contrast between the point estimate and its uncertainty is important. The treatment group had a higher observed improvement percentage than the untreated-control group, but the recalculated risk-difference interval includes no difference and extends in both directions. This illustrates why a point estimate should be read together with its interval rather than treated as a definitive description of the underlying effect.

The record also permits comparison of two statistical scales: the sponsor’s odds ratio and unadjusted recalculations from the posted summaries. The sponsor’s interval crosses the odds-ratio value for no association, as do the recalculated ratio intervals. The differences among scales underline the value of identifying whether a result is expressed as an absolute difference or a relative measure.

Finally, the planning illustrations show how strongly sample-size requirements depend on the effect targeted and the desired power. They are not a reconstruction of the trial’s original design. The registry’s lack of reported detail on the original sample-size rationale, multiplicity, and missing-data handling limits evaluation of how the primary result fits within the complete prespecified analysis strategy.

18. 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’s primary analysis population excludes randomized participants who did not have baseline photographs of acceptable quality, but the number excluded and reasons are not reported in the registry record. The handling of missing Day 90 photographs, unavailable assessments, or other missing primary-outcome data is also not reported. The posted primary comparison therefore cannot by itself show how sensitive the result is to those issues.

The endpoint is based on evaluator classification. The record identifies three blinded evaluators and the rule requiring at least two to judge improvement, but it does not report evaluator agreement, the process for resolving disagreements, or how ungradable photographs were handled. The specific masking roles are not reported in the registry record, despite the study being identified as single-masked.

The registry does not report the trial’s original sample-size calculation, detailed statistical analysis plan, multiplicity procedure, interim analyses, or method for the sponsor’s odds-ratio analysis. The sample-size illustrations use the observed effect and stated planning assumptions, not the original design rationale. The absence of these details limits assessment of whether the posted analysis matches a prespecified plan.

Secondary outcomes are listed, but their quantitative results are not reported in the registry record. The primary assessment is at Day 90, and longer-term outcome results are not reported in the registry record. Safety information is presented as aggregate counts and selected serious-event terms; further event-level details and causal assessments are not reported. These limitations narrow the conclusions to the posted primary endpoint, analysis, and safety counts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Evaluation of the Effectiveness and Safety of the Ulthera® DeepSEE® System for Treating Skin Laxity in the Lower Face and Submentum — NCT04795622.
• Registry record last updated 2023-03-23; status last verified 2023-03.
• Results first posted 2023-02-15.
• 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.

22. Record Summary

NCT04795622 is a completed, randomized, single-masked, parallel-group study of the Ulthera DeepSEE System for lower-face and submental skin laxity. The registry lists an enrollment of 201, with a start date of 2021-03-16 and a primary completion date of 2022-01-18.

The primary outcome was the percentage of participants judged improved at Day 90 from baseline and Day 90 photographs. Improvement required at least two of three blinded evaluators to judge the photographs improved. The full analysis set included randomized participants with acceptable-quality baseline photographs.

The observed improvement percentages were 54.2% for treatment and 47.0% for untreated control. The unadjusted risk-difference estimate was 0.072, with a confidence interval from -0.068 to 0.211 and an unadjusted p-value of 0.316. The interval includes no difference. The registry also reports a sponsor odds-ratio analysis with a 95% confidence interval that crosses the no-association value. The original sample-size rationale, multiplicity plan, and missing-data procedures are not reported in the registry record.