Phase 3 Study of Deoxycholic Acid Injection (ATX-101) Versus Placebo for the Reduction of Localized Subcutaneous Fat in the Submental Area: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase 3 Study of Deoxycholic Acid Injection (ATX-101) Versus Placebo for the Reduction of Localized Subcutaneous Fat in the Submental Area (NCT01546142), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Achieved a Composite 1-grade Response.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, placebo-controlled, parallel-group Phase 3 study of deoxycholic acid injection, also identified in the title as ATX-101, versus placebo for localized subcutaneous fat in the submental area. Kythera Biopharmaceuticals was the sponsor. The registry lists the study as completed, with a start date of 2012-03 and primary completion in 2013-05. Enrollment was 516.

The two assigned regimens used the same injection volume and treatment-session schedule. The active arm received deoxycholic acid 2 mg/cm² in 0.2 mL injections, up to 10 mL per session. The placebo arm received placebo in 0.2 mL injections, also up to 10 mL per session. Sessions were approximately 1 month apart, for up to a maximum of 6 treatments. The registry does not report whether all participants received the maximum number of treatments.

The primary endpoint was a composite response based on two ordinal rating scales. A participant had to improve at least 1 grade from baseline on both the clinician-reported and patient-reported scales. The assessment was scheduled 12 weeks after the last treatment, with the stated overall timeframe extending up to 32 weeks after the first treatment. The primary population was intent-to-treat, and missing values were handled using multiple imputation.

The registry also lists an MRI response and change in the Patient-Reported Submental Fat Impact Scale as secondary outcomes. The posted record includes results for these outcomes, but it does not report the full protocol, the original sample-size justification, or detailed operational information such as the randomization procedure and any stratification factors. Those details should not be inferred from the trial title or from the statistical results.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) population; missing values were imputed using a multiple imputation process.

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: Intention-to-treat population

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Achieved a Composite 1-grade Response, measured over Baseline and 12 weeks after last treatment (up to 32 weeks after first treatment).

The primary endpoint was the percentage of participants who achieved a composite 1-grade response. To qualify, a participant needed at least a 1-grade improvement from baseline on both the Clinician-Reported Submental Fat Rating Scale and the Patient-Reported Submental Fat Rating Scale. The response was assessed 12 weeks after the last treatment, within a timeframe of baseline and 12 weeks after the last treatment, up to 32 weeks after the first treatment.

The clinician-reported scale was based on the investigator’s clinical evaluation. It used a 5-point ordinal scale from 0, absent, to 4, extreme. The patient-reported scale asked how much fat the participant had under the chin, with response options ranging from 0, no chin fat at all, to 4, a very large amount of chin fat. Each scale captures a different perspective: one is the investigator’s assessment, and the other is the participant’s own report.

Requiring improvement on both scales makes the outcome a joint threshold rather than a change on either scale alone. It was used to express the proportion meeting a defined response criterion, rather than to describe the average change in a score. The registry identifies the intent-to-treat population and says missing values were imputed using a multiple imputation process. The endpoint does not, by itself, describe the size of each participant’s change or how long a response continued after the assessment.

7. Results Posted in the Registry

• Deoxycholic Acid Injection: 66.7% (172/258) versus 22.1% (57/258) on control; risk difference 44.6 percentage points (95% CI 36.9 to 52.2), risk ratio 3.02 (2.36–3.85); 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 With a Magnetic Resonance Imaging (MRI) Response

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Deoxycholic Acid Injection: 39.8% (45/113) versus 5.4% (6/112) on control; risk difference 34.5 percentage points (95% CI 24.5 to 44.4), risk ratio 7.43 (3.30–16.72); 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 Deoxycholic Acid Injection than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Patient-Reported Submental Fat Impact Scale (PR-SMFIS)

• 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:
  • Deoxycholic Acid Injection: mean -3.48 versus -1.42 on control; difference -2.06 (95% CI -2.50 to -1.62), standardized effect d = -0.80; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Deoxycholic Acid Injection than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry posts two secondary outcomes: MRI response and change from baseline in the Patient-Reported Submental Fat Impact Scale. The posted comparisons favor the deoxycholic acid injection arm on both measures, but these endpoints assess different aspects of the outcome and use different statistical methods. Their overall direction is consistent with the primary response comparison, while their meaning remains specific to each measure.

The MRI outcome is a binary response measure, whereas the impact scale is a continuous change score. They are not alternate versions of the primary composite. The primary endpoint required a threshold improvement on both clinician- and patient-rated fullness scales; the MRI and impact-scale outcomes do not share that same response definition. Agreement in direction can provide context, but it does not make the endpoints interchangeable or demonstrate that they measure an identical effect.

Secondary outcomes generally carry less inferential weight than a designated primary outcome when the registry does not report a plan controlling the chance of false-positive findings across multiple tests. The record does not report a multiplicity adjustment or testing hierarchy for these secondary comparisons. Their p-values should therefore be read as outcome-specific, unadjusted evidence rather than as definitive family-wide tests.

The MRI outcome has fewer participants in its posted summaries than the primary outcome. The registry record does not explain the reason for that difference, so it should not be attributed to a particular missingness or assessment process. For the impact scale, the sponsor reports an ANCOVA p-value but does not report its adjusted estimate or confidence interval. These reporting limits constrain comparisons of precision across the secondary findings.

Taken together, the secondary results provide additional outcome-specific context that is directionally consistent with the primary result. They do not resolve unreported questions about multiplicity, missingness, model details, durability, or generalizability. Their role is supportive and descriptive in the registry record, rather than a replacement for the primary endpoint.

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

• Percentage of Participants With a Magnetic Resonance Imaging (MRI) Response
• Change From Baseline in Patient-Reported Submental Fat Impact Scale (PR-SMFIS)

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help interpret the registry results. The primary outcome is binary at the participant level: each participant either met the composite response definition or did not. A percentage summarizes the proportion meeting that definition in each arm. It is straightforward to read, but it depends on the exact threshold used. Here, the threshold required improvement on both rating scales, so the percentage is not the proportion improving on either scale alone.

What does a risk ratio describe?

A risk ratio compares the response proportion in one group with the response proportion in another. A value of 1 represents equal proportions under this measure. Values greater than 1 indicate a higher proportion in the group in the numerator; values less than 1 indicate a lower proportion. The registry’s sponsor-reported primary analysis gives a risk ratio of 2.983. This is a relative comparison, not an absolute difference in percentage points, and it does not mean that every participant had the same response.

A risk difference answers a different question: it subtracts one group’s response proportion from the other group’s proportion. It expresses the comparison on an absolute scale. The recalculated estimates in the statistical material use unadjusted calculations from posted summaries. They can provide a useful independent description, but they are not a replacement for the sponsor’s own analysis. Relative and absolute measures can both be informative, and their numerical scales should not be compared as though they were the same quantity.

Why can the reported and recalculated estimates differ?

The registry reports a Cochran-Mantel-Haenszel analysis for the primary risk ratio. The recalculation is an unadjusted comparison based on the posted summary statistics. An adjusted or stratified method and an unadjusted method need not produce identical estimates or confidence intervals. The registry record does not report the strata or other details needed to reproduce the reported method fully. There is no flagged discrepancy between the posted sponsor analysis and the recalculated result, but the sponsor’s reported method remains the primary record of its analysis.

A confidence interval describes a range of estimates compatible with the observed data under the statistical method and its assumptions. Its width reflects statistical precision: a narrower interval indicates less sampling uncertainty than a wider interval on the same scale. A confidence interval is not a guarantee that the true value lies within the specific interval, and it does not incorporate every possible source of uncertainty, such as measurement limitations or unreported design details.

What does the p-value contribute?

The reported p-value is p < 0.001. Under the null comparison and the assumptions of the analysis, a p-value this small indicates that data at least as incompatible with the null would be uncommon. It does not measure effect size, practical importance, or the probability that a result is due to chance. Nor does it account for the number of outcomes examined unless the analysis explicitly addresses multiplicity. The registry record does not report an adjustment for the secondary outcome comparisons.

For the change in the Patient-Reported Submental Fat Impact Scale, the outcome is continuous rather than binary. The posted group summaries are means with standard deviations. A mean describes the average score change, while a standard deviation describes the spread of participant-level changes around the mean. The sponsor reports an ANCOVA analysis with p < 0.001, but the registry does not post an adjusted estimate or confidence interval for that analysis. The unadjusted recalculation based on the group summaries is not the same as an ANCOVA result, which can account for baseline values and other model terms; those details are not reported in the registry record.

Why can over-dispersion matter?

For count outcomes, over-dispersion occurs when variability is greater than a model assumes. A model that understates variability can produce intervals that are too narrow and tests that are too optimistic. That general concern is not directly the central issue for this primary binary response, which is analyzed as a proportion, but it illustrates why the chosen statistical model should match the outcome and its variability. The registry’s posted primary analysis is a risk-ratio analysis, not a count-rate model.

For binary outcomes, precision depends in part on the number of observed responses and nonresponses in each group. For continuous outcomes, precision depends on the group sizes and variability. These are general statistical principles; they do not reveal the study’s original design assumptions, which are not reported in the registry record. The sample-size illustrations use the observed effects and stated planning assumptions, rather than documenting the original design calculation.

The primary analysis population is intent-to-treat, meaning the registry identifies participants according to the assigned study groups for that analysis. The record states that missing primary outcome values were imputed using multiple imputation. In general, multiple imputation uses a statistical model to create plausible values for missing observations, analyzes the resulting completed datasets, and combines their results to reflect imputation uncertainty. The registry does not report the imputation model, variables included, number of imputations, or sensitivity analyses. Thus, the label alone cannot establish whether missingness assumptions were reasonable.

Finally, multiple outcomes create a multiplicity question. If several endpoints are tested, the chance of at least one apparently notable result can increase when each is assessed independently. An adjustment or a prespecified hierarchy can address that issue, but such details are not reported in the registry record. The primary result and secondary results should therefore be distinguished rather than treated as a single collection of equivalent tests.

11. Confidence Intervals and Precision

The sponsor-reported primary risk ratio is 2.983, with a 95% confidence interval from 2.311 to 3.849. The interval is entirely above the value representing equal response proportions under a risk ratio. This indicates that the reported analysis is compatible with a range of relative response contrasts, not a single exact value. The interval does not show the absolute difference in response proportions; that is a separate statistical measure.

The primary arm percentages, 66.5% and 22.2%, give the observed response proportions in the registry’s posted primary population. Those percentages are point estimates: they describe the analyzed data but are subject to sampling variability. The sponsor’s interval applies to the reported risk ratio, not directly to each displayed percentage. The registry does not provide confidence intervals for the arm percentages in the primary outcome record.

A confidence interval’s width is one way to assess precision on its own scale. It should be interpreted together with the estimate and the outcome definition. A relatively precise estimate can still be affected by limitations that a confidence interval does not include, such as errors in measurement, missing-data assumptions, or the applicability of the enrolled population to other settings. Statistical precision is not the same as certainty about every aspect of the result.

The secondary MRI response comparison has a sponsor-reported risk ratio of 7.838, with a 95% confidence interval from 3.299 to 18.622. The interval is wider on the relative scale than the primary risk-ratio interval, indicating greater uncertainty around that secondary estimate. The MRI outcome has fewer participants in its posted arm summaries than the primary outcome. This comparison should be interpreted as a secondary finding, with the additional caution that the registry does not report a multiplicity adjustment.

The sponsor’s posted ANCOVA result for the patient-reported impact scale gives p < 0.001, but no adjusted estimate or confidence interval is reported. The unadjusted recalculation has an interval for the mean difference, but it is not the sponsor’s ANCOVA interval. Precision for the sponsor’s adjusted comparison cannot be fully assessed from the reported p-value alone.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size illustrations describe hypothetical future planning based on fractions of the observed effect. For these outcomes, the figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect. These calculations are illustrations based on the observed result, not the trial’s original design calculation; the original sample-size assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the assumptions were correct. The 90% power column gives the corresponding per-arm number for a design with a 90% chance. Power is a design property calculated before results are observed; it is not a measure of how likely the observed result is to be true.

Rows planning for 100% of the observed effect use the full observed effect as the target. Rows planning for 75% or 50% use smaller target effects. Smaller effects are harder to distinguish from random variation and therefore require more participants per arm to achieve the same planned power, all else equal. This relationship is a general planning principle and is reflected in the increasing illustrative sample sizes as the target effect becomes smaller.

These values are not observed power. They do not establish that the completed trial was adequately or inadequately designed, because the registry does not report the original design assumptions. They are conditional planning calculations, and changing assumptions about the effect, allocation, significance level, analysis, or outcome could change the resulting sample-size needs.

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 = 0.221; treatment proportion p₁ = 0.667; average p̄ = 0.444.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7026 = 1.3771.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6280 = 0.5285.
4. n = (1.3771 + 0.5285)² / (0.4457)² = 18.3, rounded up to 19 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 <- 0.22093023255814                          # control proportion
p1 <- 0.666666666666667                          # 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(1546142)
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 = 19 (80% power), 24 (90% power)
 75% of observed effect: n per arm = 33 (80% power), 43 (90% power)
 50% of observed effect: n per arm = 69 (80% power), 92 (90% power)
power.prop.test: 18.3 
Simulated power at n = 19 per arm: 0.823 (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 the sponsor’s primary comparison as a Cochran-Mantel-Haenszel risk ratio of 2.983, with a 95% confidence interval from 2.311 to 3.849 and p < 0.001. The recalculated comparison uses the posted group summaries and is unadjusted. It is a separate descriptive calculation, not a reconstruction of every feature of the sponsor’s analysis.

The reported result and recalculation address the same broad contrast in primary response, but they use different summary measures and methods. The sponsor reports a relative measure, the risk ratio; the recalculation also includes an absolute risk-difference measure. Differences in scale and adjustment mean these estimates should not be expected to match numerically. The registry record does not provide the strata or other analysis details needed to independently reproduce the Cochran-Mantel-Haenszel result.

No discrepancy is flagged between the posted sponsor analysis and the recalculated comparison. The sponsor’s own analysis is therefore the main reported inferential result. The recalculation is useful as a transparent, unadjusted check based on the available summaries, but it should not be treated as more authoritative than the sponsor’s stated analysis or as evidence that the sponsor used an unadjusted method.

For the continuous secondary outcome, the sponsor reports ANCOVA and p < 0.001, without an adjusted effect estimate or interval. Its recalculated mean difference is based on posted group summaries and is likewise not a substitute for the adjusted analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and posts two secondary outcomes. It does not report whether the secondary tests were adjusted for multiplicity, arranged in a formal testing hierarchy, or treated as exploratory. When multiple outcomes are tested, independent unadjusted tests can increase the chance of at least one apparently notable result even when no underlying difference exists across the family of outcomes. This general issue is why the secondary p-values should not automatically be interpreted as though each were the sole prespecified test.

The primary outcome uses an intent-to-treat population, and the registry states that missing values were imputed using a multiple imputation process. This is important information because an analysis of a binary response requires an outcome classification for participants included in the analysis. Multiple imputation is a method for handling missing data by estimating plausible values under a model and incorporating uncertainty from that process. It does not eliminate the need for assumptions about why data are missing and how missingness relates to observed information.

The registry record does not report the imputation model, variables used, number of imputed datasets, assumptions about the missingness process, or sensitivity analyses comparing alternative assumptions. It is therefore not possible to assess from the record alone how robust the primary result is to different missing-data scenarios. The registry also does not specify the missing-data handling for each secondary outcome.

The record does not report a full statistical analysis plan, the original sample-size justification, interim analyses, or whether any outcome definitions or analyses changed during the study. Those details should not be inferred from the completed status or from the statistical significance of the posted results. Their absence limits independent evaluation of prespecification and the consequences of missingness or multiple testing.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: diverticulitis (0.4%), influenza (0.4%), spinal cord infection (0.4%), breast cancer (0.4%), hip surgery (0.4%).

The registry lists serious adverse events affecting 7 participants in the deoxycholic acid injection group and 10 in the placebo group. The serious-event risk sets are 258 and 256, respectively. These counts describe the registry’s reported serious adverse event summary; they do not identify whether events were considered related to treatment. The registry lists deaths as not reported in the record.

For other adverse events, the registry lists 251 participants affected in the injection group and 216 in the placebo group, with risk sets of 258 and 256. These are aggregate figures, and the record does not provide a complete event-by-event account in the information summarized. The labels and counts should not be interpreted as a comparison of severity or causation without further detail.

The registry lists six serious-event terms, each reported as 0.4%: Diverticulitis, Influenza, Spinal cord infection, Breast cancer, Hip surgery and Vaginal operation. These terms describe reported events; the record does not establish that the study intervention caused them. The serious adverse event figures are descriptive and do not, by themselves, establish comparative safety.

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

The results describe how the randomized groups compared on registry-defined outcomes at the specified follow-up. For the primary endpoint, the reported response proportion was higher in the deoxycholic acid injection group than in the placebo group, and the sponsor’s risk-ratio interval was above the value representing equal response proportions. The posted secondary comparisons were also directionally consistent, though they have their own definitions and limitations.

The primary endpoint is a threshold measure requiring improvement on both clinician- and patient-reported rating scales. It does not express the average amount of change, the full range of responses, or how an individual participant’s outcome might differ from the group result. The assessment timing also bounds the interpretation: the endpoint concerns the stated follow-up after the last treatment, not an unreported longer-term period.

These statistics do not establish that every participant benefited, that the result applies to people outside the enrolled population, or that the same results would occur under different treatment schedules or settings. They also do not answer all questions about safety, durability, or how participants valued the changes. The registry does not report enough detail to evaluate all design and analysis assumptions independently.

A statistically small p-value does not mean that the result is free from bias or that its practical significance is settled. The confidence interval captures sampling uncertainty under the reported analysis, not every form of uncertainty. Missing-data assumptions, multiplicity, outcome measurement and unreported analysis details remain relevant to interpretation.

The findings should be understood as statistical evidence from a particular randomized, double-blind, placebo-controlled study, not as individualized medical advice. The registry record gives a bounded account of outcomes and comparisons; it does not resolve decisions for a particular person or establish conclusions beyond the measures and timeframe it reports.

18. Why This Trial Matters Statistically

This trial is statistically informative because its primary outcome combines two perspectives on submental fullness: an investigator rating and a participant rating. Requiring improvement on both makes the endpoint more specific than a response on either scale alone. It also means that the reported percentage answers a precise threshold question, which should be kept in view when interpreting the result.

The randomized, double-blind, placebo-controlled, parallel-group design provides a structured comparison between the intervention and a placebo regimen. The posted primary result includes both arm response proportions and a sponsor-reported risk ratio with a confidence interval and p-value. Considering the absolute group proportions alongside the relative comparison helps readers distinguish how common the response was in each arm from how the proportions relate to one another.

The record also illustrates why analysis method matters. The sponsor’s reported Cochran-Mantel-Haenszel analysis and an unadjusted recalculation are not identical procedures or measures. Clear separation of the sponsor analysis from recalculated summary-statistic comparisons helps avoid treating a convenient calculation as though it were the original trial analysis.

Finally, the registry contains secondary outcomes, a stated multiple-imputation approach for missing primary values, and adverse-event summaries, but leaves important methodological details unreported. That combination shows why statistical interpretation requires attention not just to p-values, but also to outcome definitions, precision, missing data, multiplicity and the limits of registry reporting. The result is most useful when read as a defined comparison with a defined follow-up, rather than as a universal or complete account of every possible outcome.

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 design the trial. The planning illustrations based on observed effects cannot fill that gap. Nor does the record provide the full protocol or statistical analysis plan, so prespecification of all outcomes and methods cannot be independently assessed from the registry information.

For the primary outcome, missing values were imputed using multiple imputation, but the imputation model and assumptions are not reported. No sensitivity analyses for missing data are described in the record. The degree to which the result might change under other missing-data assumptions is therefore not established by the posted information.

The record does not report whether or how multiplicity was controlled for secondary outcomes. It also omits details needed to reproduce the reported Cochran-Mantel-Haenszel and ANCOVA analyses fully. In particular, the adjusted estimate and confidence interval for the ANCOVA result are not posted. The recalculated summaries do not substitute for those missing sponsor-analysis details.

The MRI response summaries include fewer participants than the primary summaries, but the registry does not state why. The primary outcome’s threshold definition also compresses potentially different degrees of improvement into a response category, and the posted result does not describe the distribution of individual changes. Finally, the follow-up assessment is at the specified time after treatment; longer-term outcomes are not reported in the record. These limitations constrain claims about durability, broader applicability and the full clinical meaning of the measured differences.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Phase 3 Study of Deoxycholic Acid Injection (ATX-101) Versus Placebo for the Reduction of Localized Subcutaneous Fat in the Submental Area — NCT01546142.
• Registry record last updated 2015-06-15; status last verified 2015-05.
• Results first posted 2015-06-15.
• 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.

23. Record Summary

The registry record describes a completed randomized, double-blind, placebo-controlled, parallel-group Phase 3 trial sponsored by Kythera Biopharmaceuticals. It enrolled 516 participants with moderate or severe submental fullness and compared deoxycholic acid injection with placebo. The listed study dates are 2012-03 for start and 2013-05 for primary completion.

The primary outcome was a composite 1-grade response on both clinician- and patient-reported submental fat rating scales. The sponsor reported a risk ratio of 2.983, with a 95% confidence interval from 2.311 to 3.849 and p < 0.001. Missing primary outcome values were handled using multiple imputation in the intent-to-treat population.

The registry also reports MRI response and patient-reported impact-scale outcomes, as well as serious adverse event summaries. It does not report several details needed for a full independent assessment, including the original sample-size justification, complete missing-data assumptions and multiplicity procedures.