Research on Optimizing the Use of Technology With Education: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Research on Optimizing the Use of Technology With Education (NCT05564481), a randomized na study. The primary outcome is Glycemic Control.

2. Clinical Question

3. Trial Design

This was a randomized, single-masked, parallel-group study listed as completed. The registry reports enrollment of 60 participants and identifies the study as a feasibility trial. The sponsor was Children's National Research Institute. The study start date was 2022-09-07, and primary completion was 2025-01-01. The phase is listed as NA.

The two assigned groups differed in when they received the behavioral intervention. The immediate-intervention group was assigned three video-conferencing sessions with a Certified Diabetes Care and Education Specialist interventionist and connection with a peer parent consultant after randomization. The expected duration was 3 mo. The wait-list/delayed group was assigned no intervention during the first 6 months after randomization, followed by the intervention. Thus, the primary comparison at 6 months concerns immediate intervention versus a period of delayed intervention, not intervention versus a permanently untreated group.

The registry identifies the design as parallel and randomized, but does not report the randomization sequence, allocation concealment, or the identity of the person or people masked. The record does not say whether the statistical analysis followed an intention-to-treat principle, how participants were handled if they did not follow their assignment, or whether the analysis adjusted for baseline values or other characteristics. Those details are not reported in the registry record.

The primary outcome was assessed at 6 months post-randomization. The registry also lists secondary outcomes concerning family conflict, CGM benefits and burdens, and child or teen diabetes distress. It reports 22 outcome measures and 16 posted secondary outcomes. The outcome summaries include results for a subset of secondary measures, but a complete account of all measurement procedures and analysis methods is 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: 148 dyads were assessed for eligibility. Of those, 88 were excluded. 20 of those were due to losing contact before being able to enroll, 64 were ineligible per the phone screen, 2 had an exclusionary medical illness, and 4 were enrolled but not randomized. Of the 4 dyads who did not get randomized, 1 did not complete baseline and 3 did not start their CGM, which was an inclusion criterion. The enrollment number \& number of participants Started/Completed represents the number of family dyads.

Overall Study

Analysis population for the primary outcome, as defined in the registry: HbA1c was collected only for youth participants in each dyad, not caregivers. 26 A1c values were collected for each intervention group at the primary outcomes timepoint. There were some missing data, which account for the difference in N between Baseline and 6 Months.

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: The immediate intervention had 31 dyads (31 youth, 31 caregivers) totaling 62 participants. The delayed intervention had 29 dyads (29 youth, 29 caregivers) totaling 58 participants. This is a total of 60 dyads (120 individual participants).

6. Primary Endpoint

The registry lists the primary outcome as Glycemic Control, measured over 6 months post-randomization.

The primary endpoint was glycemic control measured by hemoglobin A1c (HbA1c), expressed as a percentage, at 6 months post-randomization. HbA1c is used as a measure of average blood glucose over time. In a trial examining support intended to optimize continuous glucose monitor use, it provides a clinical outcome related to glycemic control, rather than a direct measure of whether a participant began or consistently used a monitor. The registry lists HbA1c as the primary outcome and identifies the reported summary as a mean with standard deviation.

The outcome was collected only for youth participants in each dyad, not for caregivers. The registry says that 26 A1c values were collected for each intervention group at the primary outcome timepoint and notes some missing data, accounting for a difference between the baseline and six-month sample sizes. The number of missing values and the baseline sample sizes are not reported in the registry record. The posted six-month summaries give a mean of 10.05 with standard deviation 2.0 for immediate intervention and a mean of 10.34 with standard deviation 2.002 for wait-list/delayed intervention.

HbA1c is relevant to the study's stated aim, but the registry record does not report a direct primary endpoint for CGM uptake, duration of use, or adherence. Consequently, the primary result describes HbA1c at follow-up and should not be treated as a direct measure of technology uptake.

7. Results Posted in the Registry

• Wait-list/Delayed Intervention: mean 10.34 versus 10.05 on control; difference 0.28 (95% CI -0.80 to 1.37), standardized effect d = 0.14; z-test p = 0.609.

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.

Caregiver-Reported Family Conflict

• 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:
  • Wait-list/Delayed Intervention: mean 28.04 versus 27.41 on control; difference 0.63 (95% CI -3.89 to 5.16), standardized effect d = 0.08; z-test p = 0.784.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Wait-list/Delayed Intervention and the control. The interval gives the range of effects that remain compatible with the data.

Youth-Reported Family Conflict

• 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:
  • Wait-list/Delayed Intervention: mean 27.48 versus 28.31 on control; difference -0.83 (95% CI -5.70 to 4.04), standardized effect d = -0.09; z-test p = 0.739.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Wait-list/Delayed Intervention and the control. The interval gives the range of effects that remain compatible with the data.

Child/Teen Diabetes Distress

• 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:
  • Wait-list/Delayed Intervention: mean 42.66 versus 48.16 on control; difference -5.50 (95% CI -16.56 to 5.56), standardized effect d = -0.27; z-test p = 0.329.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Wait-list/Delayed Intervention and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover family conflict reported separately by caregivers and youth, as well as child or teen diabetes distress and CGM benefits and burdens. The registry lists 16 posted secondary outcomes, while detailed summaries are available for only some of these measures. The posted comparisons do not all point in the same direction: the caregiver- and youth-reported family-conflict estimates have opposite signs, and the diabetes-distress estimate also has a different direction from one of those reports. The registry does not state how higher scores should be interpreted for every measure, so directions alone should not be called favorable or unfavorable.

The confidence intervals for the detailed secondary comparisons span zero. They therefore do not precisely establish the direction of those differences. This general pattern of uncertain secondary estimates is consistent with the primary result in one important respect: neither set of posted summaries gives a precise separation between groups. It does not, however, establish that the secondary outcomes track HbA1c or that they measure the same underlying concept. Family reports, distress scores, CGM experiences, and HbA1c address distinct aspects of the study.

Secondary outcomes are usually interpreted with caution when many outcomes are examined, because the chance of finding an apparently notable result can increase across multiple comparisons. The registry does not report a multiplicity adjustment, a hierarchy of secondary hypotheses, or which outcomes were prespecified for formal testing. The reported secondary p-values are unadjusted, and the registry does not report formal secondary analyses. For those reasons, these outcomes are best treated as descriptive and exploratory rather than as independent confirmatory evidence for the primary comparison.

The record does not provide detailed results for every posted secondary outcome in the summaries described. Readers should not infer that an outcome with no detailed summary had no change, no effect, or an unfavorable result. Its result and analysis details are not reported in the registry record.

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

• Caregiver-Reported Family Conflict
• Caregiver-Reported Family Conflict
• Youth-Reported Family Conflict
• Youth-Reported Family Conflict
• Caregiver CGM Benefits and Burdens
• Caregiver CGM Benefits and Burdens
• Youth CGM Benefits and Burdens
• Youth CGM Benefits and Burdens

9. Statistical Interpretation

10. Statistical Methods Explained

General: what a mean describes. A mean is the arithmetic average of the observed outcome values in a group. Here, the primary outcome is continuous HbA1c, and the registry reports a group mean and standard deviation for each randomized group at 6 months post-randomization. The mean gives a concise description of the group's central value, but it does not show the full distribution, the range of individual values, or how outcomes changed within individual participants.

General: what a standard deviation describes. A standard deviation describes how dispersed individual observations are around their group mean. It is not the uncertainty in the mean itself and is not a confidence interval. The primary standard deviations were 2.0 for immediate intervention and 2.002 for wait-list/delayed intervention. The closeness of these reported spreads indicates similar observed dispersion in the two groups, but does not establish that the underlying distributions are identical.

General: interpreting a mean difference. A difference in means compares the group averages on the outcome's original scale. The primary estimate is reported as wait-list/delayed intervention minus immediate intervention, so a positive estimate means the observed average in the delayed group was higher. The posted means are 10.34 and 10.05, respectively, and the posted mean difference is 0.284. The direction of a numerical difference is not, by itself, a judgment about its clinical importance. That judgment requires context about the outcome and a threshold for meaningful change, neither of which is reported in the registry record.

General: confidence intervals. A confidence interval represents the uncertainty around an estimated quantity under the method used to construct it. It gives a range of values reasonably compatible with the data and method, rather than a range containing a known proportion of individual participant outcomes. The primary interval extends on both sides of zero. This means the posted data do not precisely distinguish a positive mean difference from a negative one. The width reflects limited precision; it should not be interpreted as proof that all values inside the interval are equally plausible or that values outside it are impossible.

General: p-values. A p-value describes how unusual data at least as incompatible with a specified null model would be if that model and the test assumptions held. It is not the probability that the null hypothesis is true, nor is it a measure of the size or importance of an effect. The registry labels the primary p-value as unadjusted and reports 0.609. Without a stated analysis plan, distributional checks, or details of the test, the value should be read as a reported unadjusted comparison rather than as a complete account of the statistical evidence.

General: standardized effects. A standardized effect expresses a difference relative to a measure of outcome variability, allowing effects measured on different scales to be described on a common scale. The comparison record contains a standardized effect estimate, but its interpretation depends on the chosen standardization and assumptions. It does not replace the mean difference in HbA1c units, and it does not state whether an observed difference is important to participants. The registry does not report a clinically meaningful threshold for HbA1c in this study.

General: group sizes and standard errors. The amount of information available for estimating a group mean depends in part on the number of observed participants and the variability of their measurements. More observations can generally improve precision when other factors are similar. The registry reports 26.0 participants in each group for the primary outcome and notes missing data relative to baseline. It does not provide enough detail to reconstruct the participant flow or determine how the missing values were handled. Standard errors are included in the comparison record, but the registry does not describe the inferential procedure that uses them.

General: over-dispersion. Over-dispersion occurs when the observed variability is greater than a statistical model assumes. It can make uncertainty estimates too small if the model does not account for the extra variability. This is a general concern in some types of outcome data; the primary outcome is continuous, and the registry does not report a model-based analysis or an over-dispersion assessment. Therefore, no claim about over-dispersion in this trial is warranted.

General: randomized comparisons. Random assignment is intended to make groups comparable on average at the start of a study, including for characteristics that may not have been measured. It does not guarantee identical groups, especially in a feasibility study with limited enrollment. A comparison at follow-up can be influenced by missing outcomes, deviations from assigned intervention, and analytic choices. The registry identifies randomized allocation but does not report the allocation procedure, adherence, baseline-adjusted analysis, or analysis population. Those omissions prevent a fuller assessment of how the randomized design was carried through in the reported result.

General: feasibility and estimation. A feasibility trial can describe whether study procedures and intervention delivery can be conducted and can provide preliminary outcome estimates. The registry calls this study a feasibility trial and states that the intervention was designed to optimize CGM use in adolescents from underrepresented populations in diabetes technology research. The registry does not report specific feasibility criteria or whether they were met. The posted outcome estimates therefore provide preliminary information, but do not by themselves establish the precision or design requirements for a later confirmatory study.

11. Confidence Intervals and Precision

The primary estimate is a mean difference of 0.284, with the comparison defined as wait-list/delayed intervention minus immediate intervention. Its confidence interval extends below and above zero. That range means the observed data do not locate the group difference precisely enough to rule out values in either direction. The interval is not narrow enough to support a precise estimate of the underlying difference, and the point estimate should not be read in isolation.

Precision depends on the outcome variability and the amount of observed information. The registry reports 26.0 outcome values in each group, with standard deviations of 2.0 and 2.002. It also notes some missing data relative to baseline. The baseline counts, the number of missing values, and the approach used to address missingness are not reported in the registry record. These details would help readers evaluate the effective information available for the primary comparison and possible sensitivity of the result to missing outcomes.

A confidence interval and a p-value answer related but different questions. The interval describes uncertainty about the size and direction of the difference, while the unadjusted p-value of 0.609 summarizes compatibility with a null comparison under the test's assumptions. Neither statistic establishes equivalence or clinical importance. The registry does not report an equivalence margin, a clinically meaningful difference, or the original precision target for the study.

Because the interval encompasses both negative and positive differences, the data leave substantial uncertainty about the direction as well as the magnitude of the contrast. This uncertainty should be kept in view alongside the feasibility purpose and incomplete reporting of the analysis methods.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial's original design assumptions. For continuous outcomes, the listed counts are participants per arm. The registry's assumptions for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each scenario uses the stated fraction of the observed effect as the effect to detect. The original sample-size justification and design assumptions are not reported in the registry record.

The primary-outcome illustration gives 780 participants per arm for 80% power and 1,044 participants per arm for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, it gives 1,386 participants per arm for 80% power and 1,855 participants per arm for 90% power. For 50% of the observed effect, it gives 3,118 participants per arm for 80% power and 4,173 participants per arm for 90% power. These are planning illustrations based on the posted estimate and its variability, not counts required by the trial's protocol.

In general, power is the probability that a planned statistical test will detect an effect of a specified size if that effect is present, under the planning assumptions. The 80% and 90% columns therefore describe different target chances of detecting the stated effect. The 90% target requires more participants than the 80% target in the listed scenarios. A smaller effect is harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants. The curve should be read in the same way: it represents how the planning requirement changes as the effect size changes, subject to the stated assumptions.

This is not observed power. It is a planning exercise using the observed effect as an input, and it does not show the probability that the trial's result is correct or the probability that an effect exists. The original study's sample-size rationale is not reported in the registry record.

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 = 0.284; pooled standard deviation σ = 2.001.
2. n = 2 × (1.96 + 0.842)² × 2.001² / 0.284² = 779.3, rounded up to 780 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 <- 0.283999999999999                      # observed difference in means
sigma <- 2.00100024987505                     # 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(5564481)
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 = 780 (80% power), 1,044 (90% power)
 75% of observed effect: n per arm = 1,386 (80% power), 1,855 (90% power)
 50% of observed effect: n per arm = 3,118 (80% power), 4,173 (90% power)
power.t.test: 780.2 
Simulated power at n = 780 per arm: 0.800 (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 registry lists 22 outcome measures and 16 posted secondary outcomes. Testing or interpreting many outcomes can create multiplicity concerns: even when no underlying differences exist, a collection of comparisons can produce isolated results that appear unusual. A prespecified testing hierarchy or an adjustment for multiple comparisons can help clarify how evidence across outcomes should be interpreted. Neither a multiplicity strategy nor a hierarchy is reported in the registry record. The secondary p-values are labeled unadjusted.

The record includes posted group summaries and comparisons, but reports 0 analyses and no reported secondary analyses. It does not describe a statistical analysis plan, the tests used, covariate adjustment, model diagnostics, or rules for selecting the analysis population. It is therefore not possible to determine from the registry record whether the posted comparisons follow a prespecified plan, whether any outcomes were analyzed as secondary exploratory measures, or how choices among analyses were handled.

Missing primary outcome data are explicitly noted. The registry says that 26 A1c values were collected for each group at the six-month primary outcome timepoint and that some missing data account for the difference between baseline and six months. The number of missing observations, reasons for missingness, baseline sample counts, and missing-data methods are not reported in the registry record. No imputation method or sensitivity analysis is described. Missingness can affect estimates if participants with observed outcomes differ systematically from those without them; the record does not provide enough information to assess that possibility.

The registry does not report whether participants were analyzed according to their randomized group, whether all randomized participants were included, or how departures from the assigned intervention were handled. An intention-to-treat analysis population, a per-protocol population, and any other analysis population are not described. The identity of the masked party is also not reported. These gaps do not change the posted descriptive values, but they limit evaluation of the analysis process and the robustness of the comparisons.

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.

The safety record separates youth and caregiver groups and reports serious adverse events, other adverse events, and deaths. For immediate-intervention youth, 31 were at risk and 0 had a serious adverse event, 0 had another adverse event, and 0 deaths were reported. For the wait-list/delayed-intervention youth group, 29 were at risk and the corresponding counts were 0, 0, and 0. The caregiver groups had the same reported counts by assignment: 31 at risk in immediate intervention and 29 in wait-list/delayed intervention, with 0 serious adverse events, 0 other adverse events, and 0 deaths in each group.

These figures describe events recorded in the registry during the reported safety period. They do not establish that no adverse experiences occurred outside the event categories or reporting period, and they do not quantify the precision of the event rates. The registry does not report event definitions, collection procedures, follow-up duration for safety reporting, or a detailed assessment of causality. The absence of reported events should therefore be read as a description of the posted safety counts, not as proof of no risk.

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

The posted results describe outcomes in a randomized feasibility trial of education and parent coaching support intended to optimize CGM use among adolescents with type 1 diabetes. At six months, the average HbA1c values were close in the two groups, and the reported mean difference was 0.284. The confidence interval includes values on either side of zero, and the unadjusted p-value was 0.609. Taken together, these figures describe an uncertain between-group estimate rather than a precise conclusion about the direction or size of a difference.

The result does not establish that immediate intervention and delayed intervention are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether the plausible differences fall within that margin; neither is reported in the registry record. Nor does the result establish that the intervention has no effect. The interval's breadth leaves room for effects in either direction, and the study enrolled 60 participants overall, with 26.0 observed at the primary timepoint in each group.

The primary endpoint measures HbA1c, not CGM initiation, sustained use, or adherence. Even if HbA1c is relevant to the study's aims, its result cannot by itself establish whether the intervention changed technology uptake. The registry does not report a primary numerical result for CGM uptake or duration of use in the posted primary comparison.

The record also does not report the original sample-size justification, detailed analysis methods, missing-data strategy, or multiplicity plan. Some primary outcome data were missing, and the registry does not explain how the missing observations were handled. These reporting limitations restrict conclusions about precision and robustness. The secondary results address different outcomes and are unadjusted, so they should not be treated as a substitute for a clear primary analysis.

Overall, the registry provides preliminary group summaries and an uncertain primary comparison. It does not support a definitive claim of benefit, no effect, equivalence, or harm. Interpreting the result requires keeping the feasibility purpose, the limited observed outcome counts, missing-data note, and incomplete analytic reporting in view.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized design and a numerical treatment contrast do not automatically produce a precise answer. Randomization supports a fair comparison in principle, but the amount of observed outcome information and the variability of the measure determine how tightly the effect can be estimated. In this study, the primary confidence interval spans zero and allows differences in either direction, so the point estimate alone would give an incomplete picture.

It also illustrates the distinction between a feasibility study and a confirmatory evaluation. The registry calls the study a feasibility trial and describes an intervention aimed at a population underrepresented in diabetes technology research. Its primary result can contribute preliminary information, but the registry does not report feasibility criteria, the original sample-size rationale, or a formal analysis plan. Those missing details make it difficult to judge how the study's original goals map to the posted outcome analysis.

The endpoint choice matters as well. HbA1c is a measure of glycemic control, whereas the intervention's stated aim concerns optimizing CGM use. The primary endpoint is relevant to health outcomes, but it is not itself a direct measure of CGM uptake or continued use. Statistical interpretation should distinguish the intervention's rationale from the specific outcome measured.

Finally, the record shows why precision, missing data, and multiplicity belong in the same interpretation. The primary outcome had missing values, and the registry does not describe their handling. Numerous outcomes are listed, while no multiplicity plan is reported. These are not reasons to dismiss the posted results; they are reasons to treat the comparisons as limited evidence and to distinguish descriptive findings from a prespecified confirmatory conclusion.

18. Limitations

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

The registry record provides limited detail about participant characteristics, eligibility criteria, and representativeness. The study is described as targeting hard-to-reach adolescents and underrepresented populations in diabetes technology research, but the characteristics of enrolled participants are not reported in the information available for these results. This limits assessment of how well the findings apply to other adolescents with type 1 diabetes.

The primary endpoint is HbA1c, while the intervention is intended to optimize CGM use. The posted primary outcome does not directly report CGM uptake or sustained use. Although secondary outcomes include CGM benefits and burdens, detailed summaries for those measures are not included among the results. The registry record does not report whether participants initiated or continued CGM during follow-up.

The primary outcome description notes missing data, but the number of missing values, reasons for missingness, baseline counts, and analytic handling are not reported. The record also does not describe adherence to the intervention, fidelity of delivery, or whether the delayed group received the planned later intervention. These omissions constrain interpretation of what exposure the group comparison represents in practice.

Statistical reporting is incomplete for evaluating the comparisons. The analysis plan, exact tests, adjustment strategy, analysis population, multiplicity approach, and sensitivity analyses are not reported in the registry record. The identity of the masked party and details of allocation concealment are also not reported. The primary confidence interval is broad, and the comparison is based on 26.0 observed participants in each group. Together, the limited precision and reporting gaps mean the posted estimates should be regarded as preliminary rather than definitive.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Research on Optimizing the Use of Technology With Education — NCT05564481.
• Registry record last updated 2026-10-22; status last verified 2026-07.
• Results first posted 2026-10-22.
• 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

NCT05564481, titled Research on Optimizing the Use of Technology With Education, is a completed randomized, single-masked, parallel feasibility trial sponsored by Children's National Research Institute. It enrolled 60 participants and compared immediate diabetes education and parent coaching support with a wait-list/delayed intervention. The primary outcome was youth HbA1c at 6 months post-randomization.

The posted primary means were 10.05 for immediate intervention and 10.34 for wait-list/delayed intervention, with a reported mean difference of 0.284 and an unadjusted p-value of 0.609. The confidence interval spans zero, indicating substantial uncertainty about the direction and size of the difference. Some primary data were missing. Details on missing-data handling, the original sample-size rationale, the statistical analysis plan, and multiplicity are not reported in the registry record. The results are best read as preliminary estimates from a feasibility study, not as a definitive conclusion about efficacy or equivalence.