Effect of Omega-3 Fatty Acids Supplementation on Hypertriglyceridemia in Pediatric Patients With Obesity.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of Omega-3 Fatty Acids Supplementation on Hypertriglyceridemia in Pediatric Patients With Obesity. (NCT03216057), a randomized na study. The primary outcome is Percentage Change in Serum Triglyceride Levels From Baseline to Week 12 of Study Treatment.

2. Clinical Question

The registry record identifies safety and efficacy as objectives, but the posted primary endpoint is specifically a laboratory measure: percentage change in serum triglycerides. It therefore addresses the between-group contrast in this measure over the stated treatment period. It does not, by itself, answer questions about longer-term outcomes or outcomes other than those recorded.

The record lists 168 participants as enrolled, while the posted primary outcome data report 65 participants in each treatment group. It describes the primary analysis population as an intention-to-treat population comprising subjects who received at least one dose. The record does not provide further participant-flow details in the information reported for this analysis.

3. Trial Design

The registry describes a randomized, double-blind, parallel-group, placebo-controlled clinical trial. Participants were assigned to omega-3 fatty acids or placebo. The record identifies the trial as completed and lists phase as not applicable. The sponsor was Hospital Infantil de Mexico Federico Gomez.

The intervention was omega-3 fatty acids at 3 grams per day for 12 weeks. The arm description says that each capsule contained 400 mg of eicosapentaenoic acid and 200 mg of docosahexaenoic acid, with five capsules allocated per day. The placebo capsules contained 600 mg of soybean oil each, with five capsules allocated per day for the same 12-week period. Both arms therefore involved a capsule regimen, although the active ingredients differed.

The registry summary describes the study population as adolescents with obesity and hypertriglyceridemia, with eligibility triglyceride levels of ≥ 150 mg/dl and ≤ 1000 mg/dl. The enrollment figure is 168. For the primary endpoint, the posted arm summaries each report 65 participants, and the stated analysis population includes subjects who received at least one dose.

The primary endpoint was percentage change in serum triglyceride levels from baseline to week 12. Secondary outcomes listed in the record include percentage and milligram changes in cholesterol, HDL-C, glucose, and uric acid. Numerical results are posted for some, but not all, listed secondary outcomes. Details about the original sample-size justification, allocation procedure, masking procedures, and any planned interim analyses 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: First of all, the researcher has enrolled 168 subjects, who were assessed for eligibility, but 38 subjects have done screen failure because they have not met all the inclusion criteria, therefore only 130 subjects, who have started the study, were randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention to treat population (All subjects who received at least one dose of intervention were assessed in statistical analysis)

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 Percentage Change in Serum Triglyceride Levels From Baseline to Week 12 of Study Treatment, measured over 12 weeks.

The primary endpoint is percentage change in serum triglyceride levels from baseline to week 12 of study treatment. It expresses the change relative to a participant’s baseline level rather than as an absolute concentration change. The registry reports the endpoint as a continuous measure, with group means and standard deviations, and identifies the timeframe as 12 weeks.

This endpoint matches the stated objective of evaluating omega-3 supplementation in adolescents with obesity and hypertriglyceridemia. Comparing mean percentage changes between the randomized groups summarizes the difference in the average change over the treatment period. The primary outcome is not a count of participants reaching a threshold, nor is it a clinical event outcome; it is a laboratory measure of triglyceride change.

The posted primary summaries report a mean percentage change of -39.1 in the omega-3 group and -14.6 in the placebo group, with 65 participants reported in each group. The registry also reports an intention-to-treat population defined as all subjects who received at least one dose. The record does not provide further details about how baseline values, missing measurements, or individual percentage changes were handled in the sponsor’s analysis. The result should therefore be read as a comparison of the posted group summaries and reported analysis, not as evidence about outcomes beyond this endpoint and timeframe.

7. Results Posted in the Registry

• Omega-3: mean -39.10 versus -14.60 on control; difference -24.50 (95% CI -32.51 to -16.49), standardized effect d = -1.05; 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 Change in Serum Cholesterol Levels From Baseline to Week 12 of Study Treatment

• 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:
  • Omega-3: mean -2.90 versus 6.10 on control; difference -9.00 (95% CI -15.90 to -2.10), standardized effect d = -0.45; z-test p = 0.011.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Omega-3 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Milligram Change in Serum Cholesterol Levels From Baseline to Week 12 of Study Treatment

• 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:
  • Omega-3: mean 157.40 versus 162.40 on control; difference -5.00 (95% CI -15.68 to 5.68), standardized effect d = -0.16; z-test p = 0.359.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Omega-3 and the control. The interval gives the range of effects that remain compatible with the data.

Percentage Change in Serum HDL-C Levels From Baseline to Week 12 of Study Treatment

• 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:
  • Omega-3: mean 3.80 versus 16.20 on control; difference -12.40 (95% CI -21.01 to -3.79), standardized effect d = -0.50; z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Omega-3 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes covering cholesterol, HDL-C, glucose, and uric acid, each described in percentage-change and milligram-change terms from baseline to week 12. Numerical group results and comparisons are available for percentage change in cholesterol, milligram change in cholesterol, and percentage change in HDL-C. Results for the other listed secondary outcomes are not reported in the registry record.

Across the posted numerical secondary results, the pattern is not uniform across measures. The recalculated percentage-change comparisons for cholesterol and HDL-C have negative mean differences, while the milligram-change cholesterol estimate is also negative but its confidence interval spans zero. This broad pattern is not a replacement for reading each endpoint on its own scale or considering the registry’s own analysis. These secondary outcomes are distinct from the primary triglyceride endpoint and do not redefine the primary result.

The registry reports two-sided comparisons for the secondary outcomes. The recalculated unadjusted p-values are not adjusted for the number of outcomes considered. When multiple outcomes are tested, the chance of observing at least one apparently notable result by chance can increase. This is a general multiplicity concern; the registry record does not report a multiplicity adjustment or a prespecified hierarchy for interpreting these secondary tests. Consequently, individual unadjusted secondary p-values carry less weight than a single prespecified primary comparison and should be considered exploratory unless the analysis plan says otherwise. That analysis plan is not reported in the registry record.

The secondary results provide additional descriptive information about measured laboratory changes, but they do not establish a consistent overall effect across all listed outcomes. The number of secondary outcomes with posted numerical results is limited relative to the full list, and the record does not provide an explanation for outcomes without numerical results. No conclusion about those unreported results can be drawn from their absence.

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

• Percentage Change in Serum Cholesterol Levels From Baseline to Week 12 of Study Treatment
• Milligram Change in Serum Cholesterol Levels From Baseline to Week 12 of Study Treatment
• Percentage Change in Serum HDL-C Levels From Baseline to Week 12 of Study Treatment
• Milligram Change in Serum HDL-C Levels From Baseline to Week 12 of Study Treatment
• Percentage Change in Serum Glucose Levels From Baseline to Week 12 of Study Treatment
• Milligram Change in Glucose Levels From Baseline to Week 12 of Study Treatment
• Percentage Change in Serum Uric Acid Levels From Baseline to Week 12 of Study Treatment
• Milligram Change in Serum Uric Acid Levels From Baseline to Week 12 of Study Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: each participant’s serum triglyceride percentage change is summarized using a mean and standard deviation. A mean describes the arithmetic average in a group. A standard deviation describes how spread out individual values are around that average. The reported means give the group-level direction and magnitude of change, while the spread indicates that participants’ values varied within each group.

What does the mean difference represent?

The reported contrast is the mean difference between the omega-3 and placebo groups. Its sign depends on the subtraction order; the posted comparison is omega-3 minus placebo. A negative estimate therefore means the omega-3 group’s mean percentage change was lower than the placebo group’s mean percentage change. This contrast is not a percentage reduction calculated by dividing one group mean by another. It is the difference between the two reported mean percentage changes.

The registry reports a two-sided t-test for the primary comparison, with the parameter described as a net mean difference. A t-test evaluates how compatible the observed difference in group means is with a null comparison of no mean difference, under the test’s assumptions. “Two-sided” means that departures in either direction are considered. The registry gives the sponsor’s result as -24.5, with a 95% confidence interval from -32.7 to -16.2 and p <0.01. The recalculation uses the posted group means and standard deviations as a simple unadjusted comparison. It gives -24.5, a 95% confidence interval from -32.51 to -16.49, and p < 0.001.

Why report both an estimate and an interval?

A single estimate provides a point summary, but it does not convey how uncertain that estimate is. A confidence interval gives a range of estimates compatible with the observed data under the specified method. A narrower interval indicates greater precision than a wider interval for the same type of estimate. The interval does not describe the range of individual participant outcomes, and it is not a probability statement about the true value.

A p-value describes the compatibility of the data with a null hypothesis under the test assumptions. It is not the probability that the null hypothesis is true, nor does it measure clinical importance. Reading the p-value alongside the estimated difference and its confidence interval is more informative than treating a threshold alone as a complete interpretation. The registry reports the primary test as a superiority analysis.

What does the recalculation add?

The recalculation is an unadjusted comparison derived from posted summary statistics. It is useful as a transparent check of the group means and reported variability, but it is not a substitute for the trial’s own analysis. It does not incorporate unreported covariate adjustment, missing-data methods, or other model details. In this case, the registry record does not flag a discrepancy between the sponsor’s reported estimate and the recalculated estimate. The recalculated interval and p-value are close to, but not identical to, those in the registry’s analysis.

The recalculation uses a pooled standard deviation of 23.3 and reports a standardized effect estimate of -1.052. A standardized effect expresses a mean difference relative to the variability scale, which can help describe magnitude in standard-deviation units. Such a standardized measure does not replace the endpoint’s original units or establish clinical importance. The registry does not provide a threshold for interpreting a clinically important change in this population.

Why can spread and distribution matter?

Mean-based methods summarize central tendency, but their interpretation depends on the data and analysis assumptions. General statistical guidance is that unusually skewed distributions, influential observations, or unequal variability can affect how well a simple mean comparison represents the data. Over-dispersion is a concern in settings where observed variability is greater than a model expects; it can make standard errors too small if not handled appropriately. That concept is general and does not establish that over-dispersion occurred in this trial. The registry record does not report distributional checks or diagnostics for the primary endpoint.

Randomization supports a between-group comparison by assigning participants to groups through a chance process, but it does not eliminate uncertainty or guarantee that every observed group characteristic is balanced. The record identifies the allocation as randomized and the design as parallel, but details of the randomization method and concealment are not reported in the registry record.

The intention-to-treat population is described as all subjects who received at least one dose of intervention. This definition is stated in the registry, but it does not include further detail about whether all randomized participants were included, how participants with unavailable week-12 measurements were handled, or how partial data were used. Those details matter because missing outcome data can affect estimates if availability is related to treatment or outcome. The registry record does not report the missing-data approach for the primary outcome.

11. Confidence Intervals and Precision

The registry’s primary estimate is a mean difference of -24.5 percentage points, with a 95% confidence interval from -32.7 to -16.2. The recalculated unadjusted estimate is also -24.5, with a 95% confidence interval from -32.51 to -16.49. Both intervals are on the negative side of zero, and their limits are close, though not identical. The sponsor’s reported interval is the result from the registry’s own analysis; the recalculation is a separate summary-statistic calculation.

In general, a 95% confidence interval describes the range produced by a method that, under its assumptions and repeated use, would contain the target parameter in 95% of such intervals. It is not a statement that there is a 95% probability that the true effect lies in this particular interval. The interval reflects sampling uncertainty under the analysis; it does not account automatically for unreported biases, measurement limitations, or analytic choices.

The interval width gives a sense of precision: a narrower interval leaves a smaller range of values compatible with the analysis, while a wider interval leaves more uncertainty about magnitude. Here the interval does not include zero, but it still spans a range of possible negative differences. The point estimate is not the only plausible value, and the data do not establish a single exact effect size.

The arm summaries report 65 participants in each group. Precision depends not only on group size but also on variability and the analysis method. The posted standard deviations are 24.7 for omega-3 and 21.8 for placebo. These describe variation in percentage changes within each group and help contextualize the uncertainty around the contrast. Confidence intervals do not tell how much individual participants’ outcomes overlap, nor do they show the range of observed outcomes.

The confidence interval is specific to the primary endpoint, its definition, and the reported 12-week comparison. It should not be carried over to secondary endpoints, safety outcomes, or longer-term effects. The registry does not report an original precision target or a minimum clinically important difference, so statistical precision alone cannot determine whether the observed difference is important in a clinical sense.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design calculation. For this continuous outcome, the figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm for a future study to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the planning model are correct. The 90% power column gives the corresponding number for a 90% chance. Power is a design-stage probability under assumptions; it does not say whether the observed trial result was correct or whether a particular conclusion is certain.

The rows consider planning for 100%, 75%, and 50% of the observed effect. As the target effect becomes smaller, it is harder to distinguish from random variation, so the planning estimate requires more participants per arm. This relationship explains why the smaller-effect scenarios have larger sample-size estimates. The figures use the variability and effect observed in this trial, so they are illustrative rather than guarantees for a future study.

These estimates are not observed power. They should not be read as a retrospective measure of the trial’s ability to detect its result. They are conditional planning values that depend on the stated assumptions, including equal group allocation, the normal approximation, and the effect fraction selected.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -24.500; pooled standard deviation σ = 23.295.
2. n = 2 × (1.96 + 0.842)² × 23.295² / -24.500² = 14.2, rounded up to 15 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -24.5                      # observed difference in means
sigma <- 23.2951711734428                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3216057)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 15 (80% power), 19 (90% power)
 75% of observed effect: n per arm = 26 (80% power), 34 (90% power)
 50% of observed effect: n per arm = 57 (80% power), 76 (90% power)
power.t.test: 15.2 
Simulated power at n = 15 per arm: 0.789 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a two-sided t-test. It gives a net mean difference of -24.5, a 95% confidence interval from -32.7 to -16.2, and p <0.01. The simple unadjusted recalculation from the posted group summaries gives the same point estimate, -24.5, with a 95% confidence interval from -32.51 to -16.49 and p < 0.001. The record does not flag a discrepancy.

The two sets of results are similar in their central estimate and overall direction, but their interval limits and p-value formats are not identical. The sponsor’s analysis is the trial’s reported inferential result. The recalculation is a separate check based on the posted means and standard deviations, without additional adjustments or information that may have been used in the sponsor’s analysis. It should not be treated as a correction to the registry result.

The record does not report enough analysis detail to explain every difference between the two presentations. In particular, unreported modeling, data handling, and rounding choices cannot be inferred from the summaries. The reported analysis and recalculated result should therefore remain clearly distinguished rather than combined into a single claim.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when investigators evaluate more than one outcome or perform multiple statistical tests. Even if each test uses the same nominal significance threshold, considering many results can increase the chance that at least one appears statistically notable by chance. This general issue is relevant because the registry lists multiple secondary outcomes and reports analyses for several of them in addition to the primary triglyceride endpoint.

The registry record does not report a multiplicity adjustment, a hierarchy for testing outcomes, or a statistical analysis plan specifying how secondary findings were intended to be interpreted. The posted secondary p-values therefore should be read as unadjusted evidence for their individual comparisons, not as family-wise controlled results. The primary endpoint remains distinct from the secondary analyses, but the record does not report whether any formal procedure protected its interpretation from other testing.

Missing-data handling is also important for interpreting continuous outcomes. The record defines the primary analysis population as subjects who received at least one dose of intervention, but does not describe how unavailable week-12 measurements were handled, how many measurements were missing, or whether any imputation or other missing-data method was used. The enrollment figure is 168, while the primary arm summaries report 65 participants per group. The record does not explain participant disposition or the relationship between enrollment and those outcome counts, so no reason for the difference can be inferred.

Analysis populations can affect results because different inclusion rules can change which participants contribute data. The stated population definition does not, on its own, establish how every randomized participant was treated in the analysis. The registry record does not report a separate per-protocol analysis or further details about exclusions.

Interim analyses, stopping rules, and the original statistical analysis plan are not reported in the registry record. Their absence from the record does not establish that such procedures were or were not used. These reporting gaps limit assessment of the complete analysis process and should be kept separate from the numerical result that is posted.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports serious adverse events for 65 participants at risk in each arm. No serious adverse events were reported in either group. It also reports zero deaths in each group. For other adverse events, the record reports 27 affected participants in the omega-3 group and 4 in the placebo group, with 65 participants at risk in each arm.

These counts describe the posted adverse-event results; they do not establish why events occurred or whether they were caused by the assigned intervention. The registry does not list serious adverse-event terms, and it does not provide event descriptions for the other adverse events in the information. The counts should not be interpreted as a complete characterization of severity, duration, or clinical importance.

In general, safety comparisons depend on how events were defined, collected, and coded, as well as on the period of observation. The record identifies the treatment period as 12 weeks but does not report further detail about adverse-event collection or monitoring. A zero count of serious events in the posted data does not prove that serious events cannot occur, and the event counts alone do not establish an overall safety profile.

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

The primary result describes a difference in mean percentage change in serum triglycerides between the randomized omega-3 and placebo groups over 12 weeks. The posted means were -39.1 and -14.6, respectively, and the sponsor-reported mean difference was -24.5, with a 95% confidence interval from -32.7 to -16.2. The comparison is evidence about this measured laboratory endpoint in the population and analysis represented by the registry record.

The result does not establish what happened to every participant. Group averages can conceal variation, including participants whose outcomes differ from the mean. The posted standard deviations indicate spread, but the record does not provide individual-level data or the full distribution of changes.

The primary result also does not answer whether the difference persisted beyond week 12, whether it changed outcomes other than serum triglycerides, or whether it has a particular clinical importance. A clinically meaningful threshold is not reported in the registry record. The endpoint is a biomarker measure, and conclusions about outcomes not measured would go beyond the posted data.

The trial record reports a randomized, double-blind, parallel-group comparison, which provides a framework for comparing the assigned groups. Nonetheless, important details about the randomization process, missing data, and analysis plan are not reported. Those omissions limit assessment of how fully the analysis reflects the randomized groups and how robust the result is to analytic choices.

Secondary outcomes and adverse-event counts provide additional context, but they should not be merged into a single conclusion. Some secondary results are not reported, and the reported secondary comparisons are unadjusted. The safety figures report no serious adverse events and no deaths in either group, alongside other adverse-event counts; these observations do not by themselves establish causality or comprehensive safety. The findings are therefore best understood as a 12-week comparison of the posted primary laboratory measure, with uncertainty and reporting limitations kept in view.

18. Why This Trial Matters Statistically

This trial illustrates how a continuous primary endpoint can be communicated using group means, standard deviations, a mean difference, a confidence interval, and a hypothesis test. Each statistic answers a different question: the means describe group summaries, the difference expresses the contrast, the interval conveys precision, and the p-value describes compatibility with a null comparison under the test assumptions. None of these alone captures every aspect of the evidence.

It also demonstrates the importance of keeping the sponsor’s analysis distinct from a recalculation based on posted summary statistics. Here, the point estimates agree, while the confidence limits and p-values differ slightly. A recalculation can help readers understand the reported summaries, but it cannot reconstruct unreported modeling or data-handling choices. The registry’s analysis is therefore an important reference point alongside the transparent unadjusted comparison.

The listed secondary endpoints make multiplicity a practical interpretive issue. A collection of unadjusted tests should not be read as if each were the sole prespecified question. The registry record does not report whether a correction or outcome hierarchy was used, leaving uncertainty about the intended role of secondary findings.

Finally, the posted enrollment figure and primary analysis counts illustrate why participant flow and missing-data reporting matter. The record reports enrollment of 168 and 65 participants per arm for the primary outcome, but does not explain the flow from enrollment to those summaries. Clear reporting of analysis populations, unavailable measurements, and original planning assumptions would help readers assess precision and generalizability without relying on inference.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the original sample-size justification, so the planning illustrations based on the observed effect should not be mistaken for the trial’s design assumptions. It also does not report the statistical analysis plan, interim analyses, or stopping rules. These omissions limit assessment of whether the posted analysis followed a prespecified approach.

Participant flow is not fully explained in the information reported. Enrollment is listed as 168, while the primary arm summaries each report 65 participants. The stated analysis population includes subjects who received at least one dose, but the record does not describe exclusions, missing week-12 measurements, or how missing data were handled. The effect of any such data availability cannot be determined from the posted summaries.

The registry does not report details of randomization sequence generation, allocation concealment, or masking procedures. It identifies the study as randomized and double blind, but the practical methods used to implement these features are not described in the information reported. The record also does not provide diagnostic checks for the mean-based analysis or further details about distributional assumptions.

Numerical results are not reported for every listed secondary outcome, and no multiplicity adjustment or hierarchy is described. The adverse-event information includes counts but no serious-event terms and limited descriptions of other events. A clinical-importance threshold for the primary outcome is not reported. These trial-specific reporting gaps constrain interpretation of secondary findings, safety, precision, and the clinical meaning of the observed laboratory difference.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effect of Omega-3 Fatty Acids Supplementation on Hypertriglyceridemia in Pediatric Patients With Obesity. — NCT03216057.
• Registry record last updated 2025-03-18; status last verified 2025-03.
• Results first posted 2025-03-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed randomized, double-blind, parallel-group, placebo-controlled trial of omega-3 fatty acids in adolescents with obesity and hypertriglyceridemia. It lists enrollment of 168 and compares omega-3 at 3 grams per day with soybean-oil placebo over 12 weeks.

The primary endpoint was percentage change in serum triglycerides from baseline to week 12. The posted arm means were -39.1 for omega-3 and -14.6 for placebo, with 65 participants reported per arm. The sponsor’s reported mean difference was -24.5, with a 95% confidence interval from -32.7 to -16.2 and p <0.01.

The registry lists secondary laboratory outcomes and reports some numerical results, along with adverse-event counts. The original sample-size justification, detailed missing-data methods, multiplicity procedures, and several other analysis details are not reported in the registry record.