Efficacy and Safety of RZL-012 on Submental Fat Reduction: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of RZL-012 on Submental Fat Reduction (NCT04867434), a randomized phase 2 study. The primary outcome is Efficacy -Proportion of Subjects With at Least a 1-grade Improvement in the C-CAT Scale at Day 84.

2. Clinical Question

The outcome is a thresholded change in a clinician-rated scale, rather than a direct measure of the amount of fat removed. It asks whether a participant's score improved by at least one grade by the scheduled assessment. The record also includes participant-rated assessment and submental fat volume outcomes, which offer different perspectives on change. Those outcomes can support context about the primary result, but they are not interchangeable with the clinician-rated endpoint. The study's listed follow-up period for efficacy and safety was 84 days.

3. Trial Design

This was a Phase 2b randomized, double-blind, parallel-group, placebo-controlled study of RZL-012 in subjects seeking submental fat reduction. The record lists Submental Fat as the condition and Raziel Therapeutics Ltd. as the sponsor. The study began on 2021-06-15, had primary completion on 2022-04-20, and is marked completed.

The brief summary describes randomization in a 1:1:1 ratio to a single multi-injection treatment on Day 0: high-dose RZL-012, low-dose RZL-012, or placebo. The arm descriptions identify the active formulations as RZL-012 50mg/ml and RZL-012 34mg/ml. They describe 32±4 injections per treatment session. The high-dose description gives a maximum of 36 injections and a maximum dose of 270 mg; the low-dose description gives a maximum of 36 injections and a maximum dose of 183.6 mg. Placebo was vehicle delivered at each injection site, with a maximum injection volume of up to 5.4 mL for all groups.

The reported primary outcome counts are 43 in the high-dose arm, 39 in the low-dose arm, and 27 in placebo; the corresponding arm sizes are 50, 53, and 48. These are the counts and denominators posted for the primary outcome, not a description of how missing observations were handled. The record does not report the original sample-size justification, detailed randomization procedures, concealment method, blinding assessment, or the statistical analysis plan. It also does not report the analysis population definitions. The total enrollment and the brief-summary planned number of eligible subjects are both stated in the registry record and should not be treated as interchangeable descriptions of the analyzed outcome groups.

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

Analysis population for the primary outcome, as defined in the registry: The proportion of subjects who have at least a 1-grade improvement in the C-CAT on Day 84 versus baseline will be calculated for the placebo group and the RZL-012 high-dose group along with 95% Confidence interval for proportion

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.

6. Primary Endpoint

The registry lists the primary outcome as Efficacy -Proportion of Subjects With at Least a 1-grade Improvement in the C-CAT Scale at Day 84, measured over 84 days.

The primary endpoint is the proportion of participants with at least a 1-grade improvement from baseline on the Clinician Chin Assessment Tool (C-CAT) at Day 84. The record describes the CAT as a 5-point scale: 0 represents no fat, while 4 represents a very noticeable bulge and fat that extends beyond the neck. The endpoint therefore converts a clinician's assessment of change into a yes-or-no outcome: whether the participant improved by at least one grade by the specified visit.

A thresholded outcome can be easy to interpret in terms of the share of participants who reach a defined change. Comparing that share between randomized groups can describe how often the stated improvement occurred in each group over the follow-up period. However, it does not show the full distribution of score changes. Participants with a one-grade improvement and participants with a larger improvement both count as having met the threshold, while changes that do not reach the threshold are grouped together.

The registry record specifies comparison of the placebo and high-dose groups in its primary outcome population description, and the posted results include comparisons for both active-dose groups versus placebo. The endpoint is a Day 84 assessment relative to baseline; it is not a measure of long-term durability. The record does not report details such as the handling of participants without a Day 84 assessment or the exact analysis population used for the proportions.

7. Results Posted in the Registry

• RZL-012 50mg/ml: 86.0% (43/50) versus 56.2% (27/48) on control; risk difference 29.8 percentage points (95% CI 12.7 to 46.8), risk ratio 1.53 (1.16–2.01); unadjusted two-proportion z-test p = 0.001.
• RZL-012 34mg/ml: 73.6% (39/53) versus 56.2% (27/48) on control; risk difference 17.3 percentage points (95% CI -1.0 to 35.7), risk ratio 1.31 (0.97–1.76); unadjusted two-proportion z-test p = 0.068.

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.

Efficacy - the Proportion of Subjects With at Least 1-grade Improvement in Subject Chin Assessment Tool (S-CAT)

• 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:
  • RZL-012 50mg/ml: 86.0% (43/50) versus 62.5% (30/48) on control; risk difference 23.5 percentage points (95% CI 6.8 to 40.2), risk ratio 1.38 (1.08–1.76); unadjusted two-proportion z-test p = 0.008.
  • RZL-012 34mg/ml: 79.2% (42/53) versus 62.5% (30/48) on control; risk difference 16.7 percentage points (95% CI -0.8 to 34.3), risk ratio 1.27 (0.98–1.64); unadjusted two-proportion z-test p = 0.063.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for RZL-012 50mg/ml than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between RZL-012 34mg/ml and the control. The interval gives the range of effects that remain compatible with the data.

Efficacy - Relative Change in Submental Fat Volume on Day 84 vs. Baseline

• 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:
  • RZL-012 50mg/ml: mean -14.92 versus 1.45 on control; difference -16.37 (95% CI -20.34 to -12.40), standardized effect d = -1.76; z-test p = <0.001.
  • RZL-012 34mg/ml: mean -8.34 versus 1.45 on control; difference -9.79 (95% CI -14.08 to -5.50), standardized effect d = -0.95; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for RZL-012 50mg/ml than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for RZL-012 34mg/ml than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the secondary efficacy outcomes, the broad direction is generally consistent with the primary high-dose result: the active groups tend to show more favorable observed outcomes than placebo. The apparent strength of the evidence is not uniform. Some binary comparisons have intervals that include zero, while the continuous volume comparisons have intervals that exclude zero. This variation underscores that evidence depends on the endpoint's scale, variability, available observations, and uncertainty, not just whether the estimates point in a similar direction.

The participant-rated S-CAT asks whether participants report at least a 1-grade improvement, whereas the primary C-CAT outcome uses clinician assessment. Agreement in general direction can be informative because the measures reflect different assessors, but they are not the same outcome and one does not validate the other automatically. The volume outcome is a mean relative change, which uses more of the measurement scale than a thresholded improvement indicator. Its results therefore add a distinct view of change rather than a direct replication of the primary endpoint.

Secondary findings typically carry less weight than a prespecified primary result because there may be multiple outcomes and comparisons, and chance findings become more likely when many hypotheses are examined. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for interpreting these secondary tests. Their unadjusted p-values should accordingly be treated as exploratory evidence rather than as confirmatory findings with controlled overall error rates.

The safety follow-up is also listed as a secondary outcome, but event counts alone cannot summarize every aspect of tolerability. Overall, the secondary outcomes provide context and show a pattern that is not wholly at odds with the primary comparison. They do not remove uncertainty about the primary estimate or supply the unreported analysis and follow-up details needed for broader conclusions.

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

• Efficacy - the Proportion of Subjects With at Least 1-grade Improvement in Subject Chin Assessment Tool (S-CAT)
• Efficacy - Relative Change in Submental Fat Volume on Day 84 vs. Baseline
• Safety - Adverse Events Follow up

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary comparisons are differences in proportions, expressed as risk differences. A risk difference subtracts the proportion meeting the endpoint in placebo from the proportion in an active-treatment group. A value above zero therefore indicates a greater observed proportion meeting the endpoint in the active group; a value below zero indicates a lower observed proportion. The risk difference is an absolute contrast on the proportion scale, not a relative measure.

What does the confidence interval describe?

A confidence interval expresses uncertainty around an estimate using a range of values compatible with the data and the interval procedure. For the high-dose primary comparison, the risk-difference interval runs from 0.127 to 0.468 and does not cross zero. For the lower-dose comparison, the interval runs from -0.010 to 0.357 and includes zero. The latter interval is wider in relation to its estimate and leaves more uncertainty about the direction and size of the difference. A confidence interval is not a guarantee that the true effect lies inside its endpoints, nor does it describe the spread of individual participant outcomes.

How should p-values be read?

The reported p-values are unadjusted. In general, a p-value describes how unusual data at least as discrepant as those observed would be under a specified no-difference model and its assumptions. It is not the probability that the no-difference model is true, and it does not measure the magnitude or practical importance of an effect. Because the registry record does not report a multiplicity strategy, the unadjusted values should be interpreted as comparisons considered individually, not as a documented family-wise analysis.

What do the other effect measures add?

The registry calculations also report relative risks and odds ratios for the binary comparisons. These express contrasts on relative scales, unlike the risk difference. They can give a different numerical impression because they use different denominators and mathematical scales. The risk difference remains a direct statement of the absolute separation between observed proportions. No single measure fully conveys uncertainty, so the estimate and its confidence interval should be read together.

How are continuous outcomes represented?

The submental fat volume outcome is reported as a mean relative change from baseline, with standard deviations for each arm. Its comparison is a difference in means. The posted mean difference for the high-dose group versus placebo is -16.37, with a 95% confidence interval from -20.34 to -12.4; for the low-dose group, it is -9.79, with an interval from -14.08 to -5.498. The outcome is labeled as percentage of volume reduction, while arm means are negative for the active groups and positive for placebo. These units and signs should be kept in view when interpreting the contrast.

In general, a standard deviation describes variation among participant-level observations around an arm mean; it is not the uncertainty in that mean. A confidence interval for a difference in means addresses uncertainty about the contrast. The reported p-values for both volume comparisons are <0.001. These are unadjusted comparisons and do not, by themselves, resolve multiplicity or missing-data concerns.

Why does over-dispersion matter in general?

For binary outcomes, a simple model may assume that variation is fully described by the event probability and the number of observations. General statistical concept: if observations vary more than that model allows, the data are over-dispersed relative to the model. Standard errors may then be too small and intervals too narrow if the extra variation is ignored. The registry record does not state that over-dispersion was assessed or that a particular model was used; this general point should not be mistaken for a claim about the trial's analysis.

What analysis details are missing?

The registry record does not report the statistical model, covariate adjustment, missing-data method, analysis population definitions, or a full prespecified testing sequence. It lists no reported analyses for the posted endpoint summaries. The comparisons are the simple unadjusted recalculations from the posted summary statistics. The record does not flag a discrepancy, so there is no stated conflict between these recalculations and a sponsor analysis. Where a discrepancy is flagged, the sponsor's own analysis takes precedence.

11. Confidence Intervals and Precision

Precision concerns how tightly the data locate an effect estimate, not whether an estimate is important or whether a treatment should be used. For the primary high-dose risk difference, the 95% confidence interval is 0.127 to 0.468. Its endpoints are both above zero, but the range still allows materially different magnitudes of separation. The point estimate should therefore be read together with the interval rather than as an exact effect.

For the low-dose primary comparison, the interval is -0.010 to 0.357. It includes zero and also includes positive differences. The data leave more uncertainty about whether the difference is above zero and about its size. This is not proof of no difference. The two dose comparisons also have different estimated effects and intervals, but the record does not report a direct statistical comparison between the active doses.

The confidence intervals for the continuous volume outcome exclude zero for both active-dose comparisons: -20.34 to -12.4 for high dose and -14.08 to -5.498 for low dose. These interval estimates concern mean differences in that outcome, not the proportion reaching the C-CAT threshold. The distinct endpoints and scales mean that precision should be considered separately for each result.

In general, interval width depends on the amount of information and the variability in the outcome, among other features of the analysis. The registry record reports arm sizes and outcome summaries, but it does not give the analysis details needed to assess all sources of uncertainty, including missing observations or adjustment choices. Confidence intervals quantify sampling uncertainty under their calculation assumptions; they do not account automatically for every source of bias, outcome selection, or multiplicity.

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 planning illustrations express required sample sizes as participants per arm for the binary and continuous outcomes in this study, not as total events. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers an effect to detect set at 100%, 75%, or 50% of the observed effect. The original trial's own sample-size assumptions and justification are not reported in the registry record; these illustrations are not evidence of the design rationale.

The 80% power column gives the estimated participants per arm for a design that would have an 80% chance of detecting the stated effect under the calculation assumptions, if that effect and model assumptions were correct. The 90% power column uses a higher target chance of detection and consequently generally calls for more participants per arm. These are prospective planning quantities, not a description of the probability that the completed trial found a true effect.

Smaller effects require more participants to distinguish them from no difference with the same significance level and target power. The rows that use a smaller fraction of the observed effect therefore show larger sample-size requirements. This is a planning illustration based on the observed effect, not observed power. It should not be treated as a recommendation for a future study without separate clinical and design assumptions, including a defensible target effect and decisions about multiplicity and missing data.

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 = 0.562; treatment proportion p₁ = 0.860; average p̄ = 0.711.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6409 = 1.2561.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6054 = 0.5095.
4. n = (1.2561 + 0.5095)² / (0.2975)² = 35.2, rounded up to 36 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 <- 0.5625                          # control proportion
p1 <- 0.86                          # 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(4867434)
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 = 36 (80% power), 47 (90% power)
 75% of observed effect: n per arm = 69 (80% power), 91 (90% power)
 50% of observed effect: n per arm = 163 (80% power), 218 (90% power)
power.prop.test: 35.2 
Simulated power at n = 36 per arm: 0.820 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, treatment comparisons, time points, or analyses are tested. Even if each test is conducted at a conventional threshold, the chance of at least one apparently notable finding across a family of tests can increase. General statistical concept: prespecifying a primary hypothesis and controlling the testing family can help distinguish confirmatory evidence from exploratory patterns. The registry record identifies a primary outcome and lists secondary outcomes, but it does not report a multiplicity adjustment, a testing hierarchy, or how the primary and secondary hypotheses were handled together.

The posted p-values are described as unadjusted comparisons. They should therefore be read as individual tests, without assuming that their nominal values account for all comparisons. This matters for both the active-dose comparisons and the several efficacy outcomes. The record does not report whether other outcomes or analyses were examined outside the posted results, so the full testing family cannot be reconstructed from the registry entry.

Missing data can also affect an outcome proportion or mean. The reported endpoint summaries give arm sizes and outcome counts, but the registry record does not report how participants with missing Day 84 assessments were handled, whether imputation was used, or whether sensitivity analyses were conducted. It does not identify whether the denominators represent all randomized participants, participants with observed outcomes, or another analysis set. Consequently, the posted summaries should not be described as intention-to-treat or per-protocol unless that classification is documented elsewhere in the registry record.

The record does not report definitions for safety or efficacy analysis populations, protocol deviations, or a statistical plan specifying estimands and missing-data assumptions. These omissions limit assessment of how robust the comparisons are to analysis choices. They do not alter the arithmetic of the posted counts and intervals, but they constrain conclusions about how fully the summaries represent all randomized participants and how the results should be interpreted across the set of tests.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry record reports zero serious adverse events in each group: RZL-012 50mg/ml, RZL-012 34mg/ml, and placebo. It also reports zero deaths in each group. These are event counts during the reported safety follow-up, not evidence that no serious event could occur or that the groups have identical risks. With a limited number of participants and the follow-up described in the record, uncommon events may not be well characterized.

Other adverse events were reported for 49 of 50 participants in the high-dose group, 51 of 53 in the low-dose group, and 48 of 48 in placebo. These figures indicate that at least one other adverse event was recorded for nearly all participants in each group. The registry record does not provide the serious-event terms, and no top serious terms are listed. It also does not provide enough detail to compare event types, timing, severity, or causal attribution.

Counts should be interpreted with their group sizes and the scope of follow-up in mind. They do not establish comparative safety, and they do not replace a detailed review of adverse-event definitions and participant-level information.

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

The posted primary result shows a higher observed proportion meeting the Day 84 clinician-rated improvement threshold in the high-dose RZL-012 group than in placebo. Its risk-difference confidence interval lies above zero, while the lower-dose comparison has a confidence interval that includes zero. These findings describe the outcomes and uncertainty recorded for this study; they are not a general guarantee about outcomes in other populations or settings.

The endpoint is a threshold on a clinician-rated scale. It does not reveal the full amount of change for each participant, how participants valued that change, or how long any change lasted beyond the assessment period. The continuous volume outcome and participant-rated S-CAT offer additional perspectives, but differences in measurement do not make them interchangeable with the primary outcome. The study's efficacy follow-up is described through Day 84, so the registry record does not establish longer-term durability.

A statistically distinguishable estimate is not automatically a statement about clinical importance. The record does not report a threshold for a meaningful difference, and the confidence interval shows a range of plausible effects rather than a single certain magnitude. Similarly, a confidence interval that includes zero does not establish equivalence or prove that no difference exists.

The trial record also leaves key interpretive details unreported, including the original sample-size justification, missing-data handling, analysis populations, and multiplicity strategy. Those omissions matter when judging how complete and robust the evidence is. No medical advice follows from these statistical summaries. They describe a randomized comparison over the stated follow-up, with uncertainty and limitations that should remain part of any interpretation.

17. Why This Trial Matters Statistically

This trial illustrates why a result should be read through its endpoint, effect measure, and uncertainty together. The primary outcome is a binary threshold on a clinician-rated scale. Its risk difference communicates an absolute separation in the proportions meeting that threshold, while the confidence interval shows that the high-dose comparison is more clearly separated from zero than the lower-dose comparison. Looking only at counts, p-values, or the direction of an estimate would leave out important information.

The study also reports several kinds of secondary outcomes. A participant-rated threshold and a continuous volume measure capture different features of change. Their general directional consistency can add context, but differing scales, precision, and unadjusted testing mean they cannot simply be combined into a single verdict. This is a useful example of how endpoint multiplicity and measurement choices affect the strength of conclusions.

The registry's planning illustrations provide another statistical lesson: required sample size depends on the target effect. Smaller effects require more participants per arm under the stated planning assumptions. Because these illustrations use observed effects, they are not the same as the trial's original design justification or evidence of achieved power.

Finally, the posted summaries show what can and cannot be learned from registry-level data. Outcome counts, confidence intervals, and adverse-event totals permit a direct description of the recorded results. Missing analysis details—particularly for multiplicity, missing observations, and analysis populations—limit assessment of the assumptions behind those summaries. Keeping those distinctions explicit supports a more measured reading of the evidence.

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.

The registry record describes the study as double blind and randomized but does not report the randomization sequence generation, allocation concealment, or how blinding was maintained. It does not provide baseline characteristics, so the balance of groups on measured participant features cannot be assessed from these results alone. Nor does it report how many participants completed each follow-up assessment or the reasons for any missing observations.

The primary outcome depends on a one-grade threshold on the C-CAT. The record gives the scale anchors but not the distribution of individual score changes, so the range of changes within the groups cannot be examined from the endpoint counts. The primary time point is Day 84; no longer-term outcome is reported in the registry record.

There are multiple doses and several efficacy outcomes, but the record does not report a multiplicity procedure or an analysis hierarchy. The p-values are unadjusted, and the registry does not provide the original sample-size rationale or a detailed statistical analysis plan. It also does not report the analysis populations, missing-data approach, or sensitivity analyses. These omissions make it difficult to judge the robustness of the estimates to alternative analytic choices.

The safety summary provides serious-event and other-event counts, but not detailed event descriptions, timing, severity, or causal assessments. The registry lists no top serious adverse-event terms. The study's results therefore describe the recorded event counts, not a complete characterization of all possible safety differences. These limitations are specific to the information reported in this registry record and do not establish that the unreported procedures or analyses were not performed.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of RZL-012 on Submental Fat Reduction — NCT04867434.
• Registry record last updated 2023-09-28; status last verified 2021-04.
• Results first posted 2023-09-28.
• 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

NCT04867434 is a completed randomized, double-blind, parallel, placebo-controlled Phase 2b study of RZL-012 for submental fat reduction, sponsored by Raziel Therapeutics Ltd. The registry record lists enrollment of 151 and describes a single multi-injection treatment of high-dose RZL-012, low-dose RZL-012, or placebo, with efficacy and safety follow-up over 84 days.

The primary outcome was at least a 1-grade improvement from baseline on the clinician-rated C-CAT at Day 84. The reported high-dose comparison with placebo has a positive risk difference and a 95% confidence interval above zero; the lower-dose interval includes zero. Secondary efficacy outcomes generally point in a similar direction, but the record does not report a multiplicity strategy or detailed analysis methods. Serious adverse event and death counts were zero in all groups; other adverse events were reported in each group.

The registry does not report the original sample-size justification, missing-data handling, analysis populations, or full statistical plan. Results should therefore be read as posted estimates over the stated follow-up, with uncertainty and reporting limitations kept in view.