Get Social: Randomized Trial of a Social Network Delivered Lifestyle Intervention: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Get Social: Randomized Trial of a Social Network Delivered Lifestyle Intervention (NCT02646618), a randomized na study. The primary outcome is Weight.

2. Clinical Question

The study is listed as randomized and parallel, with no masking. Its stated objective concerns delivery format: a social-network-based program compared with group meetings. The primary measure is weight in pounds, recorded with a digital scale, and the outcome population is randomized participants. These details define what the posted primary comparison can address. Baseline balance can be relevant when interpreting a trial, but similarity in starting weight is not a treatment-effect estimate.

The record also lists a Smartphone device intervention, but does not identify a separate smartphone arm in the posted arm results or explain its role in the comparison. The two arms with posted primary results are Get Social and Traditional. Details such as a prespecified non-inferiority margin, the primary follow-up time for weight, and the planned analysis of change in weight are not reported in the registry record.

3. Trial Design

The registry identifies NCT02646618 as a randomized, parallel-group trial with no masking. The study is marked completed. Enrollment is listed as 329, and the registry lists University of Connecticut as sponsor. The phase is recorded as NA. The condition is weight loss. The start is recorded as 2016-04, and primary completion as 2020-02-26.

Two behavioral arms appear in the posted results. Get Social used a protected Twitter group to deliver the lifestyle intervention online. The arm description says online coaches would post daily content and engage with participants by responding to questions, addressing concerns, and encouraging engagement. Traditional used in-person weight-loss groups, with weekly, then biweekly, then monthly meetings over the schedule described in the record. Its intervention is described as based on the Diabetes Prevention Program and focused on lifestyle changes. Details beyond the posted description are not reported in the registry record.

The primary outcome record lists mean weight in pounds at baseline, measured with a digital scale. The posted arm means and standard deviations describe weight at the start of the study. They are not follow-up weights. The primary comparison is a mean difference between Traditional and Get Social; its estimate is 0.7 lbs, with an interval from -7.156 to 8.556 lbs and an unadjusted p-value of 0.861. This is a comparison of baseline values, not a comparison of weight loss or post-intervention weight.

The registry's brief summary calls the study a non-inferiority trial. The non-inferiority margin, the trial's original sample-size assumptions, and the protocol's analysis plan are not reported in the registry record. The posted results do not identify an endpoint that directly tests non-inferiority of weight change. Consequently, the stated trial objective and the available primary outcome description should be distinguished when interpreting the 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: Randomized participants

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 Weight, measured over Baseline.

The primary endpoint is weight, measured in pounds, at baseline. The record says a digital scale was used to record weight and identifies randomized participants as the outcome population. A mean is an appropriate summary for a continuous measurement when the aim is to describe the group's average value. The standard deviation describes how spread out individual measurements are around that average.

Baseline weight can characterize the groups before the intervention period and help readers understand whether they began at similar average levels. In a randomized trial, baseline measures also give context for interpreting later outcome comparisons. But a baseline-only value is not a measure of change. To estimate whether weight changed during the intervention, results would need to report a post-baseline measurement, a change from baseline, or an appropriate comparison of follow-up weight that accounts for the starting value.

The posted primary result compares the mean baseline weights in Get Social and Traditional. It does not report a post-intervention primary weight result or a weight-change estimate. The registry record does not report a primary follow-up timeframe for weight, a non-inferiority margin, or a primary analysis of weight change. Thus, the endpoint is useful for describing starting weight in the randomized groups, but it cannot by itself answer the stated question about comparative intervention efficacy.

7. Results Posted in the Registry

• Traditional: mean 215.40 versus 214.70 on control; difference 0.70 (95% CI -7.16 to 8.56), standardized effect d = 0.02; z-test p = 0.861.

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.

Time Spent During Intervention

• 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:
  • Traditional: mean 3.90 versus 3.00 on control; difference 0.90 (95% CI 0.58 to 1.22), standardized effect d = 0.61; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Traditional than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Retention at Follow-up

• 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:
  • Traditional: 91.4% (148/162) versus 94.0% (157/167) on control; risk difference -2.7 percentage points (95% CI -8.3 to 3.0), risk ratio 0.97 (0.91–1.03); unadjusted two-proportion z-test p = 0.355.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Traditional and the control. The interval gives the range of effects that remain compatible with the data.

Acceptability of the Intervention

• 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:
  • Traditional: 74.3% (104/140) versus 78.7% (100/127) on control; risk difference -4.5 percentage points (95% CI -14.6 to 5.7), risk ratio 0.94 (0.83–1.08); unadjusted two-proportion z-test p = 0.392.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Traditional and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover different dimensions of the intervention: time spent, retention, and acceptability. They do not all point in the same direction. Traditional has a higher posted mean time spent, while the posted retention and acceptability counts are numerically higher for Get Social. These contrasts concern participant engagement and reported acceptability, not weight change. They are therefore informative about aspects of implementation but do not answer the primary clinical question by themselves.

The primary result is a comparison of baseline weight, so the secondary results cannot be interpreted as corroborating or contradicting a demonstrated weight effect. The registry record does not post a primary follow-up weight comparison that could connect engagement or retention with weight outcomes. Nor does it report a planned analysis testing whether time spent, retention, or acceptability explains variation in weight change. Any such link would be speculative.

Unadjusted secondary results generally carry less evidential weight than a prespecified primary analysis. Multiple outcomes create multiple opportunities to observe apparently notable differences by chance, particularly when no adjustment strategy or hierarchy is reported. The record lists many outcome measures and analyses, but does not report a multiplicity plan. That absence does not show that no plan existed; it means the registry record does not document one.

There is also an inconsistency for the time-spent comparison: the simple unadjusted recalculation and the registry's reported two-sided t-test yield different p-values. The reason is not reported. This makes it especially important not to treat the recalculated result alone as definitive evidence about that secondary outcome. Overall, the secondary measures offer descriptive information on intervention burden and engagement, but their interpretation is limited by outcome multiplicity, uncertainty about analysis details, and the absence of a posted primary weight-change result.

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

• Cost Associated With Intervention
• Time Spent During Intervention
• Retention at Follow-up
• Acceptability of the Intervention
• Burden of Intervention
• Dietary Intake
• Change in Dietary Intake
• Change in Dietary Intake

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: weight in pounds. A group mean describes the center of a set of measurements, while the standard deviation describes variation among participants. In this record, the baseline means are 214.7 lbs for Get Social and 215.4 lbs for Traditional, with standard deviations of 36.9 and 35.8 lbs, respectively. The estimated mean difference is expressed as Traditional minus Get Social, giving 0.7 lbs. A positive estimate therefore means the Traditional group had the higher posted baseline mean.

A mean difference is an effect measure in the original unit of the outcome. This makes the estimate interpretable as a difference in pounds, rather than as a standardized score. The interval from -7.156 to 8.556 lbs conveys uncertainty around that estimate. Because it includes zero, the data are compatible with no average baseline difference as well as differences in either direction. The confidence level for this interval is not reported in the registry record, so it should not be assigned a level that the record does not state.

A p-value addresses how compatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not indicate the size or practical importance of a difference. The primary unadjusted p-value is 0.861. In this setting, it indicates little evidence against no difference in baseline mean weight. It does not show that the interventions have equal effects, because the measure is baseline rather than an intervention outcome.

What does randomization contribute?

Random allocation is intended to create groups that are comparable on average before treatment, including for factors that may not have been measured. It does not guarantee that every baseline characteristic will be identical in a particular trial. Reporting baseline values can help readers inspect the groups, but a test of baseline differences is not a test of intervention effectiveness. The registry record identifies randomization and parallel groups, but does not report the sequence-generation method, allocation concealment, or other operational details of assignment.

No masking is recorded. In a behavioral intervention comparison, participants and intervention staff may be aware of the delivery format, but the registry record does not report who, if anyone, was masked for outcome measurement or analysis. That detail should not be inferred from the general masking entry.

How should the secondary measures be understood?

Time spent is a continuous measure, reported as hours per participant at 12 months. Its arm summaries are means and standard deviations. Retention and acceptability are reported as counts of participants, so comparisons concern proportions rather than continuous averages. For a binary outcome, a risk difference expresses the difference between the proportions in the two groups. An interval around a risk difference describes uncertainty in that contrast; when it spans zero, the data do not clearly distinguish a difference from no difference under the method used.

The simple recalculations from posted summary statistics are unadjusted comparisons. They do not account for covariates, repeated measurements, clustering, or other features unless these are incorporated into the calculation, and no such adjustments are represented in these recalculations. A reported study analysis can use a different data set, model, or analysis population. For time spent, the recalculated p-value is below 0.001, but the registry's reported two-sided t-test p-value differs. The record does not describe why. This discrepancy is a reason to keep the recalculation distinct from the sponsor-reported analysis, not to silently replace one with the other.

Over-dispersion is a general concern when outcomes vary more than a model assumes. If a model assumes less variability than is actually present, standard errors can be too small and intervals too narrow. Conversely, appropriate modeling of extra variability can yield more cautious uncertainty estimates. This is a general statistical point; the registry record does not report whether over-dispersion was assessed or relevant to the posted analyses.

What is not documented?

The registry record does not report the original sample-size justification, the trial's planned statistical analysis in sufficient detail to reconstruct it, or whether there were interim analyses. It also does not report the handling of missing outcome data, the analysis population used for each result, or an adjustment plan for multiple outcomes. These omissions make it difficult to determine whether the posted analyses follow the original protocol or how sensitive results are to analytic decisions. The reported endpoint population is randomized participants, but that label alone does not establish that every randomized participant contributed data to every outcome analysis.

The trial is described as non-inferiority, but the margin and an analysis of the relevant intervention effect are not posted. Non-inferiority requires a prespecified clinical or scientific margin and an estimate precise enough to rule out effects beyond that margin. The baseline weight comparison cannot serve this purpose. The methods that would have been used to assess non-inferiority are not reported in the registry record.

11. Confidence Intervals and Precision

The primary estimate is a baseline mean difference of 0.7 lbs, and its interval extends from -7.156 to 8.556 lbs. The interval includes zero and reaches in both directions. It therefore does not isolate a single precise value for the baseline contrast. The posted point estimate is close to zero, but the interval shows why the point estimate should not be read alone: the data are also compatible with a larger baseline difference in either direction.

A confidence interval is a range of values that reflects the uncertainty of an estimate under a statistical procedure. It is not a range containing a known proportion of individual participants' weights, and it does not mean that each value in the range is equally plausible. The confidence level for the primary interval is not stated in the registry record. Its width should be considered alongside the endpoint itself: even a precise baseline comparison would still not estimate weight change or intervention efficacy.

The secondary retention and acceptability risk-difference intervals include zero, so their posted contrasts do not sharply distinguish a difference from no difference. The time-spent recalculation has an interval that excludes zero, but the registry's reported t-test result does not agree with the recalculated result. That disagreement limits how confidently the simple summary-statistic comparison can be used as an account of the trial's reported analysis.

Precision is different from statistical significance. A non-significant result may still be imprecise, and a statistically small p-value does not itself show that an estimate is important. For the primary endpoint, the main limitation is not only uncertainty: the measure is at baseline and is not the post-intervention comparison needed to address the trial's stated non-inferiority question. The record does not report the margin that would determine what degree of uncertainty is acceptable for such a conclusion.

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 original trial design. The registry record's planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is the stated fraction of the observed effect. For the continuous and binary outcomes represented, the figures are participants per arm; they are not total event counts. There are no time-to-event planning figures in these posted results.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the assumed effect under those assumptions, if that effect were truly present. The 90% power column describes the corresponding planning target for a 90% chance. Higher planned power generally requires more participants for the same assumed effect. The displayed rows scale the assumed effect to the full observed effect, 75% of the observed effect, and 50% of the observed effect. The smaller the effect a future study aims to detect, the more participants it generally needs, all else being equal.

These calculations use effects observed in this trial as inputs. They do not establish what the trial itself was designed to detect, and they are not observed power. The original sample-size justification and its assumptions are not reported in the registry record. The planning figures also depend on the statistical assumptions; changing the allocation, significance level, outcome variability, analysis method, or target effect can change the required sample size. They should therefore be read as illustrations for planning, not as evidence that the original study was adequately or inadequately sized.

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 = 0.700; pooled standard deviation σ = 36.363.
2. n = 2 × (1.96 + 0.842)² × 36.363² / 0.700² = 42,359.5, rounded up to 42,360 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 <- 0.700000000000017                      # observed difference in means
sigma <- 36.362568548403                     # 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(2646618)
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 = 42,360 (80% power), 56,708 (90% power)
 75% of observed effect: n per arm = 75,306 (80% power), 100,814 (90% power)
 50% of observed effect: n per arm = 169,438 (80% power), 226,830 (90% power)
power.t.test: 42360.4 
Simulated power at n = 42,360 per arm: 0.802 (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. Multiplicity, Missing Data and Analysis Populations

The record lists 49 outcome measures and 7 analyses, and reports 46 secondary outcomes. Multiple testing matters because examining many outcomes can increase the chance that at least one result appears notable even when there is no underlying effect. This is a general statistical concern, not a claim that any particular finding is false. A prespecified outcome hierarchy or multiplicity adjustment can help define how findings should be interpreted, but the registry record does not report such a plan.

The listed secondary measures span distinct concepts and timeframes. Their results should not be treated as interchangeable replications of one primary result. Nor should a selected secondary p-value be used to make a broad claim about the intervention without knowing whether it was prespecified and how the other analyses were handled. The registry record does not report whether the secondary analyses were confirmatory or exploratory.

Missing-data handling is also not reported in the registry record. The posted analyses identify outcome-specific denominators, and these differ across measures, but the record does not explain why data are absent for some participants or how missing observations were treated. The number contributing to a result can differ from the randomized group size because of follow-up availability, outcome measurement, or other analytic rules; the specific reasons in this trial are not reported.

The analysis population for each result is not described beyond the primary outcome's reference to randomized participants. The registry record does not say whether the reported comparisons follow intention-to-treat, per-protocol, or another approach, or how protocol deviations were handled. These details are particularly important for a non-inferiority design, where different analysis populations can affect interpretation. The record also does not report interim analyses, the original statistical analysis plan, or whether outcome analyses were adjusted for baseline values or other covariates.

These reporting gaps limit reconstruction of the prespecified inferential framework and assessment of robustness. They should be treated as unreported details, not as evidence that particular methods were or were not used. In particular, the absence of a posted multiplicity, missing-data, or population-analysis plan prevents a strong confirmatory interpretation of the secondary results.

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 lists zero serious adverse events in each arm and zero deaths in each arm. The numbers at risk for the serious-event summaries are 167 in Get Social and 162 in Traditional. These are the serious-event figures recorded for the groups; they do not establish that no event of any kind occurred.

Other adverse events are listed for 52 participants in Get Social and 49 in Traditional, with the corresponding at-risk counts recorded as 167 and 162. The registry does not provide the specific terms or descriptions for these other events in the posted summary. The counts alone do not describe event severity, timing, duration, relatedness to the intervention, or whether a participant experienced more than one event. The record also does not specify the surveillance period for these summaries.

Adverse-event counts are descriptive safety information. They should be read in light of how events were collected and classified, details not reported in the registry record. They do not establish whether an intervention caused an event, and zero serious events in the posted results should not be interpreted as proof that serious events are impossible.

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

The posted primary statistics show that the two randomized groups had similar average baseline weight: 214.7 lbs for Get Social and 215.4 lbs for Traditional. The estimated baseline difference is 0.7 lbs, with an interval spanning -7.156 to 8.556 lbs. This is a description of the groups at the start of the study. It is not evidence that the interventions produced similar weight outcomes.

The registry's stated purpose is to compare a social-network-delivered lifestyle intervention with traditional group meetings in a non-inferiority trial. To draw a non-inferiority conclusion, readers would need a prespecified margin and a suitable estimate of the intervention contrast at the relevant follow-up, with uncertainty sufficiently narrow relative to that margin. The registry record does not report the margin or a primary post-intervention weight result. The baseline comparison cannot establish non-inferiority, equivalence, superiority, or a weight-loss effect.

The posted secondary measures provide information about time spent, retention, and acceptability at their specified follow-up times. They may help describe how participants engaged with the two formats, but they do not substitute for the primary outcome question. The recalculated time-spent result also differs from the reported t-test result, and the reason for that difference is not reported. The secondary findings should therefore be read as limited evidence about the specific reported outcomes rather than as a general verdict on the interventions.

More broadly, statistical evidence is shaped by the outcome definition, timing, analysis population, and uncertainty. A small p-value does not prove an important effect, and a large p-value does not prove that two approaches are identical. For this record, the distinction between baseline measurement and treatment outcome is decisive. The information posted supports a description of starting weight and several secondary endpoints, while the comparative effect on weight remains unreported in the primary results.

17. Why This Trial Matters Statistically

This trial raises an important design and reporting issue: the outcome that is posted as primary must align with the question the trial is intended to answer. The registry describes a non-inferiority comparison of two delivery formats, but the primary result shown is baseline weight. Baseline information can characterize randomized groups, yet it cannot quantify how much weight participants lost or whether one delivery format was non-inferior to the other.

The distinction matters statistically because non-inferiority is not established by failing to find a difference. It requires a margin defined in advance and an interval for a relevant treatment contrast that rules out an unacceptable loss of effect. Without the margin and a suitable post-baseline estimate, a baseline p-value cannot be interpreted as evidence that the formats have comparable efficacy. The missing details are not technicalities; they determine what conclusion the analysis can support.

The record also illustrates why outcome families need transparent analysis plans. Measures of intervention time, retention, and acceptability can illuminate delivery and participant engagement, but multiple unadjusted comparisons can generate findings that are difficult to prioritize. In addition, the disagreement between the recalculated and reported time-spent test shows why a clear description of analytic populations and methods is valuable: summary statistics alone may not reproduce the study's reported result.

For biostatisticians and clinical researchers, the key lesson is to match interpretation to the endpoint, timeframe, and estimand actually reported. Precision, multiplicity, missing data, and the planned decision rule all matter. A study's stated objective is not a substitute for a posted result that measures that objective directly.

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.

A trial-specific limitation in the posted record is the mismatch between the stated non-inferiority objective and the primary outcome result. The primary measure is baseline weight, while no primary follow-up weight or change-from-baseline estimate is posted. The registry record also does not report a non-inferiority margin. As a result, the core comparative question cannot be assessed from the primary result shown.

The details available for the intervention descriptions are incomplete. The Get Social description ends mid-sentence in the registry record, and the posted Traditional description does not provide every component of the intervention. A Smartphone device intervention is listed, but its relationship to the two reported arms is not explained. These gaps make it difficult to reconstruct all intervention components or determine how consistently they were delivered.

The record does not report the original sample-size justification, statistical analysis plan, interim analyses, missing-data methods, or analysis populations for each outcome. These omissions limit assessment of whether analyses followed prespecified methods and how incomplete follow-up was handled. The numbers contributing to secondary outcomes differ, but reasons for those denominators are not reported.

The secondary findings also require caution because the record does not describe a multiplicity strategy, and the recalculated time-spent comparison differs from the reported two-sided t-test. The explanation for that discrepancy is not reported. Finally, the adverse-event summary does not describe event terms, timing, attribution, or surveillance procedures. These are limitations of the information reported in the registry record and should not be mistaken for proof that the underlying study did not address them.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Get Social: Randomized Trial of a Social Network Delivered Lifestyle Intervention — NCT02646618.
• Registry record last updated 2023-11-24; status last verified 2023-11.
• Results first posted 2021-05-05.
• 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

NCT02646618 is a completed randomized, parallel-group trial with no masking, sponsored by University of Connecticut. It compares the Get Social online lifestyle intervention with Traditional group meetings. The registry describes the study as a non-inferiority trial, but the posted primary endpoint is mean baseline weight.

Mean baseline weight was 214.7 lbs for Get Social and 215.4 lbs for Traditional. The estimated mean difference was 0.7 lbs, with an interval from -7.156 to 8.556 lbs and an unadjusted p-value of 0.861. These figures describe starting weight; they do not report comparative weight change or establish non-inferiority. Secondary results concern time spent, retention, and acceptability. The registry record does not report a non-inferiority margin, the original sample-size rationale, a full analysis plan, or methods for missing data and multiplicity.