Harnessing mHealth and Social Support to Improve Diabetes Related Health Behavior for Inner-city Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Harnessing mHealth and Social Support to Improve Diabetes Related Health Behavior for Inner-city Patients (NCT01945996), a randomized na study. The primary outcome is Feasibility.

2. Clinical Question

3. Trial Design

NCT01945996 is a completed, randomized, double-masked, parallel-group study sponsored by the University of Southern California. The registry lists enrollment of 44 and identifies diabetes mellitus as the condition. The study dates run from 2013-09 to primary completion in 2014-05. Its title describes an effort to harness mobile health and social support for diabetes-related health behavior among inner-city patients, and the official title specifies emergency department patients with diabetes and a family and friend network supporter.

The two arms both included TExT-MED for patients. In this discussion-MED Only arm, supporters did not receive additional messages. In this discussion-MED FANS arm, supporters received the FANS curriculum. This parallel design makes the added supporter curriculum the distinguishing feature between arms, while retaining TExT-MED for patients in both groups. The registry classifies both interventions as behavioral.

The registry summary says the intervention combination would be tested for feasibility and that the investigators hypothesized it would be feasible and acceptable to patients and loved ones. The primary outcome reported is the number of patients lost to follow-up at 3 months after enrollment. Secondary outcomes include diabetes knowledge, self-efficacy, diabetes-related problem areas, glycemic control, body mass index, and self-care activity sub-scores for diet and exercise. The record also lists 14 outcome measures and 11 posted secondary outcomes.

The registry record does not report the details of sequence generation, concealment, or which people were masked. It also does not report the original sample-size justification, the specific operational definition of feasibility beyond the stated follow-up outcome, or a detailed statistical analysis plan. Those omissions limit assessment of the intended design and analysis, even though the overall randomized, double-masked, parallel structure is recorded.

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: 14 patients dropped before randomization * Unable to identify support person = 4 * Unable to contact support person = 22 * Support person can not text = 15

Overall Study

Reasons for not completing this period:

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 Feasibility, measured over 3 months after enrollment.

The primary endpoint is the count of patients lost to follow-up at 3 months after enrollment. It is a retention measure: it describes whether patients remained available for follow-up, rather than their diabetes status or behavior. The registry presents this endpoint as a count of participants, with 3 reported for TExT-MED Only and 5 for TExT-MED FANS. Each arm has 22 participants in the posted results.

A follow-up measure is relevant to a feasibility study because retaining participants is necessary to collect study outcomes and assess whether the research procedures can be carried out. The registry summary identifies feasibility and acceptability as the investigators’ interest. However, the posted primary endpoint captures loss to follow-up alone; it is not a complete measure of acceptability, intervention use, or successful implementation. Those aspects may have been evaluated in other ways, but details are not reported in the registry record.

The comparison is expressed as a risk difference of 0.091, with a confidence interval from -0.135 to 0.317. Because loss to follow-up is an unfavorable event for retention, the direction of the difference is important: a positive difference corresponds to a larger observed event proportion in TExT-MED FANS than in TExT-MED Only. The interval includes both negative and positive values, so the posted estimate is compatible with differences in either direction. This small study’s endpoint is therefore best read as an observed feasibility signal with substantial uncertainty, not as a conclusive test of the broader intervention rationale.

7. Results Posted in the Registry

• TExT-MED FANS: 22.7% (5/22) versus 13.6% (3/22) on control; risk difference 9.1 percentage points (95% CI -13.5 to 31.7), risk ratio 1.67 (0.45–6.14); unadjusted two-proportion z-test p = 0.434.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: each patient is either counted as lost to follow-up or not. The registry reports the number of patients experiencing the event in each arm. A risk is the proportion of participants with the event, while a risk difference subtracts one arm’s risk from the other. Here the displayed comparison is TExT-MED FANS relative to TExT-MED Only, so a positive risk difference means the event proportion is higher in the FANS arm. This is an unadjusted comparison of the posted group summaries.

What does the risk difference communicate?

The risk difference expresses the contrast on an absolute scale. It describes the change in event proportion between arms rather than a relative multiplication of one arm’s risk. The estimate is 0.091, and its confidence interval runs from -0.135 to 0.317. Values below zero correspond to a lower event proportion in TExT-MED FANS; values above zero correspond to a higher event proportion. Since the interval contains zero, the data are compatible with no difference as well as differences in either direction. The interval’s span also indicates that the estimate is not precise.

How do risk ratios and odds ratios differ?

A risk ratio compares the event risks by division, whereas an odds ratio compares the odds of the event between arms. These relative measures can describe the same binary outcome on different scales. The posted risk ratio is 1.667, with a confidence interval from 0.453 to 6.138; the posted odds ratio is 1.863, with a confidence interval from 0.386 to 8.988. For both ratios, a value of one represents no relative contrast. Their intervals include that value, and their breadth reflects considerable uncertainty. For a common understanding of the event burden, the counts and risk difference may be more immediately interpretable than the relative measures alone.

What does the p-value add?

The unadjusted p-value is 0.434. A p-value describes how unusual data at least as discrepant as the observed data would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of a difference. The p-value should therefore be considered alongside the effect estimate, confidence interval, sample size, outcome definition, and study context. A large p-value does not show that the arms are equivalent, especially when the confidence interval permits a range of effects.

Why can sparse counts produce wide uncertainty?

With few observed events, changing the status of a small number of participants can materially affect the estimated event proportion. Statistical estimates based on sparse data therefore tend to be sensitive to the observed counts, and confidence intervals can be wide. This is a general feature of inference with limited event information, not evidence of a particular hidden mechanism in this trial. The counts of 3 and 5 are the basis of the displayed comparison, and the wide intervals show why the point estimates should not be read in isolation.

What does unadjusted mean in this comparison?

An unadjusted contrast compares the arms without accounting for other covariates in a regression or stratified model. Randomization is intended to support fair comparisons, but with a small study, the realized groups can still differ in participant characteristics by chance. The registry record does not report an adjusted analysis for this endpoint or enough detail to describe additional modeling. The posted risk difference, risk ratio, odds ratio, and p-value should accordingly be interpreted as summary-statistic comparisons, not as estimates adjusted for baseline characteristics.

Why is over-dispersion not the central issue for this endpoint?

Over-dispersion is a general concern when a count model assumes less variability than the data contain, often because counts vary more than the model expects. The primary outcome is reported as a participant-level event count with an arm-specific denominator, rather than as repeated event counts or a rate over varying exposure time. The main interpretive concerns are the small numbers of participants and events, the breadth of the confidence interval, and the absence of a reported detailed analysis plan. The registry record does not describe a count model or an over-dispersion assessment, so no claim about such an analysis can be made.

These statistical methods describe the posted comparison, not the original study’s full analysis plan. The sponsor’s own analysis takes precedence if a discrepancy is identified; the record does not indicate a discrepancy for this comparison. Inferences remain limited to the reported endpoint and the recorded follow-up period. They should not be extended to the secondary outcomes or to the overall success of the intervention without their corresponding results and methods.

10. Confidence Intervals and Precision

Precision describes how narrowly the data estimate an effect. The risk difference of 0.091 has a confidence interval from -0.135 to 0.317. The interval includes zero, meaning that no difference is among the values compatible with the data under the interval procedure. It also includes negative and positive values, so it allows for either a lower or higher event proportion in TExT-MED FANS. This is a substantial range of plausible contrasts relative to the point estimate.

The relative measures reinforce that uncertainty. The risk ratio of 1.667 has a confidence interval from 0.453 to 6.138, and the odds ratio of 1.863 has a confidence interval from 0.386 to 8.988. Each interval includes its no-contrast value, and each covers markedly different possible effect sizes. These intervals do not demonstrate equivalence; equivalence would require a prespecified margin and an analysis designed to assess whether the interval lies within that margin. Such an equivalence margin is not reported in the registry record.

Confidence intervals are generally used to show the range of effect estimates reasonably compatible with the data and the method’s assumptions. They do not mean that the true effect has a specified probability of falling inside this particular interval. The width reflects limited information in the observed data, particularly when the event counts are small. The point estimate alone can give an impression of certainty that the interval does not support.

Consequently, the results do not tightly distinguish between a potentially lower event proportion in the FANS arm, little or no difference, or a higher event proportion. A larger study might yield more precise estimates, but the actual precision would depend on event frequency, design, and conduct. The posted interval is the relevant evidence for the uncertainty of this comparison; it should not be replaced by an interpretation based only on the p-value or the direction of the point estimate.

11. 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’s design calculation. They are reported as participants per arm for 80% power and participants per arm for 90% power. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The registry record does not report the assumptions used for the trial’s own original design or sample-size justification.

For planning for 100% of the observed effect, the illustration gives 282 participants per arm for 80% power and 377 participants per arm for 90% power. For planning for 75% of the observed effect, it gives 477 participants per arm for 80% power and 638 participants per arm for 90% power. For planning for 50% of the observed effect, it gives 1,016 participants per arm for 80% power and 1,359 participants per arm for 90% power. The 80% and 90% columns represent different target probabilities of detecting the specified effect under the planning assumptions, if that effect were present and the assumptions held.

The pattern illustrates a general design principle: smaller effects require more participants to detect with the same target power. These are not observed power values and do not tell how likely the current result is to be true. They are forward-looking planning quantities tied to the observed effect, which is uncertain in this study. Because the effect estimate comes from a small study and has a broad confidence interval, planning directly around it may be unstable. The figures are best treated as illustrations of how assumptions affect a future design, not as a definitive recommendation or as evidence about the trial’s original intent.

12. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.136; treatment proportion p₁ = 0.227; average p̄ = 0.182.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5455 = 1.0691.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5417 = 0.4559.
4. n = (1.0691 + 0.4559)² / (0.0909)² = 281.4, rounded up to 282 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.136363636363636                          # control proportion
p1 <- 0.227272727272727                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1945996)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 282 (80% power), 377 (90% power)
 75% of observed effect: n per arm = 477 (80% power), 638 (90% power)
 50% of observed effect: n per arm = 1,016 (80% power), 1,359 (90% power)
power.prop.test: 281.4 
Simulated power at n = 282 per arm: 0.802 (20000 replicates)

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

13. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcome topics, including diabetes knowledge, self-efficacy, diabetes-related problem areas, glycemic control, body mass index, and self-care activity sub-scores for general diet, specific diet, and exercise. The record lists 14 outcome measures and 11 posted secondary outcomes. Multiple outcome assessments create a multiplicity concern: the more effects examined, the greater the chance that at least one result may look notable by chance if no adjustment or prespecified hierarchy is used. The registry record does not report a multiplicity adjustment, a hierarchy of outcomes, or a detailed plan for interpreting the secondary analyses.

The record reports 0 analyses in its analysis listing, while a comparison for the primary follow-up outcome is displayed. The registry record does not explain the distinction between this analysis listing and the posted comparison. It also does not report a detailed statistical analysis plan, including whether the primary endpoint was assessed with a prespecified model, how covariates were selected, or how missing observations were handled for secondary outcomes. These omissions mean that the displayed primary contrast can be interpreted as an unadjusted comparison, but the full analysis process cannot be reconstructed from the record.

Loss to follow-up is itself the primary endpoint, but it also raises a separate missing-data issue for other outcomes. Patients who are not followed may have unavailable measurements, and outcome availability could affect secondary comparisons. The registry record does not report reasons for loss to follow-up, whether participants with missing measurements were included in particular analyses, or whether any imputation or sensitivity analysis was performed. It would be inappropriate to assume that missing outcomes were handled in a particular way.

The record does not define analysis populations such as intention-to-treat or per-protocol, and it does not report exclusions after randomization. The randomized design is recorded, but the extent to which the posted outcome analyses retained participants according to initial allocation is not described. These details matter for interpreting the consequences of missing follow-up and departures from assigned intervention. The registry information supports a focused reading of the reported retention counts, while leaving important questions about secondary outcome analyses unresolved.

14. 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 registry reports zero serious adverse events and zero other adverse events in both arms. For each arm, 22 participants are listed as at risk for serious adverse events and 22 as at risk for other adverse events. Deaths are reported as zero in each arm. No serious adverse event terms are listed.

These figures describe what was recorded in the registry, not proof that no adverse events occurred outside the reporting process or that an intervention is free of risk. A zero count in a study of this size gives limited information about uncommon events. The registry record does not provide event definitions, ascertainment procedures, severity details beyond the serious-event category, or a narrative discussion of safety monitoring. It also does not explain whether any events were considered related to an intervention.

The safety counts should therefore be read narrowly: no serious or other adverse events and no deaths were reported for these arms in the posted record. They do not establish a comparative safety advantage, and they do not provide enough information to characterize risks beyond the reported categories and observation captured by the study.

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

The principal finding is a difference in the recorded follow-up loss counts: 3 of 22 in TExT-MED Only and 5 of 22 in TExT-MED FANS. The unadjusted risk difference is 0.091, with a confidence interval from -0.135 to 0.317 and an unadjusted p-value of 0.434. These results describe the observed retention outcome; they do not establish a clear difference between the arms, and the interval leaves substantial uncertainty about the direction and size of any difference.

The study’s question is relevant to feasibility because it evaluates whether a supporter curriculum can be combined with patient-facing mobile health messaging. However, the primary reported measure is loss to follow-up, not a complete assessment of feasibility or acceptability. The summary states that feasibility and acceptability to patients and loved ones were of interest, but the registry does not report details for all such dimensions. Thus, the endpoint cannot be taken as a stand-alone verdict on whether the combined approach was feasible or acceptable overall.

The comparison also does not show whether TExT-MED or FANS changed diabetes-related health behavior or clinical outcomes. The registry lists secondary topics that include self-care, glycemic control, and body mass index, but the primary result is about follow-up loss. Any claim about those other outcomes would require their results, uncertainty estimates, and analysis details. The count should not be generalized to effects on diabetes management.

Finally, the estimate arises from a small randomized study with relatively few observed endpoint events and broad confidence intervals. Randomization supports a comparative design, but it does not guarantee precise estimates in a small sample. The results can inform questions for future feasibility work and study planning, while remaining too uncertain to establish equivalence, a definitive retention effect, or effectiveness of the intervention. The registry record does not report enough detail to resolve these limitations.

16. Why This Trial Matters Statistically

This trial raises a statistical distinction that matters in early intervention research: feasibility outcomes and clinical outcomes answer different questions. Loss to follow-up can indicate whether participants remain available for research assessments, while outcomes such as self-care behavior or glycemic control address what happened to participants’ health-related measures. A retention result should not be substituted for evidence on those other outcomes.

The randomized comparison is also a useful reminder that the size and precision of an estimate matter alongside its direction. The observed counts differ, but the risk-difference confidence interval includes both negative and positive contrasts. The p-value does not settle the question, and a result that does not meet a conventional significance threshold is not the same as evidence that the arms are equivalent. In small studies, uncertainty can remain large even when a point estimate appears to favor one arm.

For future planning, the sample-size illustrations show how the chosen target effect affects the number of participants needed under stated assumptions. They also demonstrate why basing a design solely on a small study’s observed effect can be precarious: that estimate is itself uncertain. Clear prespecification of the primary feasibility criteria, missing-data handling, outcome hierarchy, and analysis population would make future results easier to interpret.

The trial’s design isolates the addition of a supporter curriculum to a patient-facing intervention, rather than contrasting the mobile intervention with no intervention. That makes the contrast specific, but interpreting it still depends on complete reporting of implementation, outcome ascertainment, and analysis. The record’s limitations do not negate the descriptive information; they define what conclusions the information can reasonably support.

17. 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 posted primary outcome concerns follow-up loss at 3 months after enrollment, and the registry reports only the event counts and arm sizes for that outcome. Reasons for loss to follow-up, timing of loss, and whether loss differed in ways related to participant characteristics are not reported in the registry record. Without those details, the endpoint cannot distinguish logistical retention difficulties from other reasons for unavailable follow-up.

The trial enrolled 44 participants, and the arm-level event counts were small. The resulting confidence intervals are broad, so the estimated contrast is imprecise. The study’s own sample-size justification and original design assumptions are not reported in the registry record. The planning illustrations are based on the observed effect and should not be mistaken for evidence about the trial’s intended power.

The registry describes the study as double-masked but does not report who was masked or how masking was maintained. Because the intervention includes messages for patients and supporters, the record does not explain the practical details of masking or whether participants could infer their group. The available information is insufficient to assess those aspects of implementation.

The record lists multiple outcome measures and secondary results, but does not report a detailed statistical analysis plan, adjustment for multiplicity, or the analysis populations used. It also does not describe missing-data procedures for secondary outcomes. The displayed primary comparison is unadjusted. These reporting gaps limit assessment of the analysis beyond the posted summary statistics.

Finally, the registry’s safety information reports zero events in the listed categories but provides little detail about definitions or ascertainment. The study’s primary feasibility measure and safety counts do not establish effects on diabetes outcomes. Interpretations should remain confined to the reported retention contrast and should not be extended to broader clinical or behavioral conclusions.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Harnessing mHealth and Social Support to Improve Diabetes Related Health Behavior for Inner-city Patients — NCT01945996.
• Registry record last updated 2018-11-06; status last verified 2018-03.
• Results first posted 2018-11-06.
• 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.

21. Record Summary

NCT01945996, titled Harnessing mHealth and Social Support to Improve Diabetes Related Health Behavior for Inner-city Patients, is a completed randomized, double-masked, parallel-group study sponsored by the University of Southern California. The registry lists enrollment of 44, with study dates from 2013-09 to primary completion in 2014-05.

Both arms received TExT-MED for patients. In this discussion-MED Only arm, supporters received no additional messages; in this discussion-MED FANS arm, supporters received the FANS curriculum. The primary outcome was the number of patients lost to follow-up at 3 months after enrollment. The posted counts were 3 of 22 and 5 of 22, respectively. The unadjusted risk difference was 0.091, with a confidence interval from -0.135 to 0.317 and an unadjusted p-value of 0.434.

The result is an imprecise retention comparison, not evidence about the intervention’s effect on diabetes outcomes. The registry record does not report a detailed analysis plan, the original sample-size justification, or full missing-data procedures.