Social Media and Risk Reduction Teaching-Enhanced Reach: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Social Media and Risk Reduction Teaching-Enhanced Reach (NCT04387552), a randomized na study. The primary outcome is Number of Infants Usually Sleeping Supine in the Previous Two Weeks.

2. Clinical Question

The primary outcome is a report of usual sleep position, not a direct observation of infant behavior. The survey offered categorical responses of supine (back), prone (stomach), side, and other. The posted comparison data focus on the count of participants whose infants usually slept supine. The registry also lists exclusive supine sleep, room sharing without bedsharing, and exclusive breastmilk feeding as secondary outcomes. Together, these outcomes address reported care practices, but they do not establish why participants chose a practice or whether messages were received, read, or followed. Those details are not reported in the registry record.

3. Trial Design

The registry identifies NCT04387552 as a completed, randomized study sponsored by Boston University. It lists the study as single-masked and sequential. The meaning and implementation of the masking and sequential model labels are not described in the registry record, so they should not be taken to imply particular procedures beyond those labels.

The four arms combine prenatal and postnatal mobile health messages. One arm received safe-sleep messages in both periods and serves as the reference for the posted comparisons. The other combinations paired prenatal safe-sleep with postnatal breastfeeding messages, prenatal breastfeeding with postnatal safe-sleep messages, or breastfeeding messages in both periods. The interventions are classified as behavioral. The registry describes the study aim as improving adherence to American Academy of Pediatrics safe-sleep recommendations and improving initiation and duration of partial and exclusive breastfeeding through direct education using mobile health technologies, such as text messaging.

The registry lists enrollment as 2093, a start date of 2022-01-20, primary completion on 2025-06-07, and overall status as completed. The primary endpoint was assessed between 2 and 6 months following postnatal randomization, on average 67.7 days. The number analyzed for each arm is the number with information about infant sleep position, and those denominators differ across posted outcomes. The allocation sequence, masking procedures, recruitment settings, eligibility details, adherence measures, and original sample-size justification are not reported in the registry record. The registry lists no reported analyses for the outcomes. The comparisons discussed are unadjusted recalculations from posted summary statistics, rather than reported model-based 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.

Before assignment: There was a 2- step randomization process- prenatally to 2 arms (n=1790, 897 randomized to prenatal safe sleep/SS and 893 randomized to prenatal breastfeeding/BF) and postnatally to 4 arms (n=1775). 15 of the 1790 randomized prenatally were not randomized postnatally- 7 of the 897 randomized to safe sleep/SS due to: participant choice (6), pregnancy loss (1), and 8 of the 893 randomized to breastfeeding/BF due to: participant choice (6), changed contact (1), pregnancy loss (1).

Prenatal Randomization Into 2 Arms

Reasons for not completing this period:

Postnatal Randomization Into 4 Arms

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The number of participants analyzed in each arm reflects the total number of participants that provided information about their infant's sleep position.

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 Number of Infants Usually Sleeping Supine in the Previous Two Weeks, measured over Between 2 and 6 months following postnatal randomization, on average 67.7 days.

The primary endpoint counts participants whose infants were reported as usually sleeping supine during the previous two weeks. The assessment used an investigator-developed maternal survey, with categorical choices of supine (back), prone (stomach), side, and other. The outcome therefore captures a caregiver’s report of usual sleep position over a stated recall period; it is not a count of all sleep episodes or an independently observed behavior.

The registry’s endpoint definition uses the number of participants analyzed in each arm who provided information about infant sleep position. Consequently, the denominator for a comparison is the number with endpoint information in the relevant arms, not necessarily the enrollment listed for the trial. The number of participants with information differs by arm and by outcome.

This endpoint is used because safe sleep is a stated focus of the intervention, and supine positioning is one of the reported practices the study set out to assess. The registry also lists exclusive supine sleep as a secondary outcome. That is a narrower measure than usually sleeping supine: a participant can report usual supine sleep without reporting exclusive supine sleep. The posted results do not establish the accuracy of self-report or describe the survey’s validation. Nor do they state whether the endpoint was assessed at the same precise follow-up time for every participant; the registry gives a range and an average assessment timing.

7. Results Posted in the Registry

• Prenatal SS/Postnatal BF: 92.2% (317/344) versus 91.4% (308/337) on control; risk difference 0.8 percentage points (95% CI -3.4 to 4.9), risk ratio 1.01 (0.96–1.05); unadjusted two-proportion z-test p = 0.719.
• Prenatal BF/Postnatal SS: 89.5% (299/334) versus 91.4% (308/337) on control; risk difference -1.9 percentage points (95% CI -6.3 to 2.6), risk ratio 0.98 (0.93–1.03); unadjusted two-proportion z-test p = 0.409.
• Prenatal BF/Postnatal BF: 87.6% (305/348) versus 91.4% (308/337) on control; risk difference -3.8 percentage points (95% CI -8.3 to 0.8), risk ratio 0.96 (0.91–1.01); unadjusted two-proportion z-test p = 0.110.

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.

Number of Infants Exclusively Sleeping Supine in the Previous Two Weeks

• 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:
  • Prenatal SS/Postnatal BF: 70.0% (240/343) versus 75.4% (254/337) on control; risk difference -5.4 percentage points (95% CI -12.1 to 1.3), risk ratio 0.93 (0.85–1.02); unadjusted two-proportion z-test p = 0.114.
  • Prenatal BF/Postnatal SS: 65.9% (220/334) versus 75.4% (254/337) on control; risk difference -9.5 percentage points (95% CI -16.4 to -2.6), risk ratio 0.87 (0.79–0.96); unadjusted two-proportion z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Prenatal SS/Postnatal BF and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Prenatal BF/Postnatal SS than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Infants Exclusively Room Sharing Without Bedsharing in the Previous Two Weeks

• 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:
  • Prenatal SS/Postnatal BF: 69.8% (240/344) versus 72.3% (243/336) on control; risk difference -2.6 percentage points (95% CI -9.4 to 4.3), risk ratio 0.96 (0.88–1.06); unadjusted two-proportion z-test p = 0.463.
  • Prenatal BF/Postnatal SS: 71.6% (232/324) versus 72.3% (243/336) on control; risk difference -0.7 percentage points (95% CI -7.6 to 6.1), risk ratio 0.99 (0.90–1.09); unadjusted two-proportion z-test p = 0.838.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Prenatal SS/Postnatal BF and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Prenatal BF/Postnatal SS and the control. The interval gives the range of effects that remain compatible with the data.

Number of Infants With Exclusive Breastmilk Feeding in the Previous Two Weeks

• 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:
  • Prenatal SS/Postnatal BF: 30.5% (106/347) versus 34.1% (116/340) on control; risk difference -3.6 percentage points (95% CI -10.6 to 3.4), risk ratio 0.90 (0.72–1.11); unadjusted two-proportion z-test p = 0.317.
  • Prenatal BF/Postnatal SS: 31.8% (107/337) versus 34.1% (116/340) on control; risk difference -2.4 percentage points (95% CI -9.4 to 4.7), risk ratio 0.93 (0.75–1.15); unadjusted two-proportion z-test p = 0.512.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Prenatal SS/Postnatal BF and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Prenatal BF/Postnatal SS and the control. The interval gives the range of effects that remain compatible with the data.

Across the secondary endpoints, the posted recalculations do not show a uniform pattern across message combinations. Exclusive supine sleep has a comparison with an interval excluding zero for prenatal breastfeeding followed by postnatal safe-sleep messaging, while the other posted comparison for that endpoint has an interval that includes zero. The room-sharing-without-bedsharing comparisons and the exclusive-breastmilk-feeding comparisons have intervals that include zero. This overall pattern is mixed rather than consistently pointing in one direction across outcomes.

The secondary outcomes add context to the primary result because they assess related but distinct reported practices during the previous two weeks. Exclusive supine sleep is narrower than usually sleeping supine; room sharing without bedsharing concerns a different sleep practice; and exclusive breastmilk feeding concerns feeding. They are not interchangeable measures and should not be treated as a single composite of safe care or intervention success. The primary endpoint’s intervals include zero, while the secondary results do not create a consistent pattern that resolves its uncertainty.

The secondary comparisons are unadjusted, and the registry lists no reported analyses for them. When multiple outcomes and pairwise comparisons are examined, the chance of at least one apparently notable result can increase. No multiplicity adjustment or prespecified hierarchy for these outcomes is reported in the registry record. Therefore, an isolated unadjusted result carries less weight than a result supported by a prespecified analysis that accounts for the set of comparisons. These results are best treated as exploratory signals to interpret alongside their uncertainty, rather than as definitive evidence.

The secondary endpoint counts also use outcome-specific denominators. A difference in the number with data across outcomes can affect precision and may reflect missing information, but the reasons and handling are not reported. It is not possible to assume that the participants contributing to one endpoint are exactly those contributing to another. The broad takeaway is variation across endpoint and arm comparisons, with limited basis in the registry record for strong conclusions about any one secondary finding.

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

• Number of Infants Exclusively Sleeping Supine in the Previous Two Weeks
• Number of Infants Exclusively Room Sharing Without Bedsharing in the Previous Two Weeks
• Number of Infants With Exclusive Breastmilk Feeding in the Previous Two Weeks

9. Statistical Interpretation

10. Statistical Methods Explained

The posted comparisons are risk differences between each intervention combination and the arm receiving prenatal and postnatal safe-sleep messages. A risk is the proportion of participants counted for the endpoint among those with endpoint information in that arm. A risk difference expresses the absolute contrast between those proportions. Positive values indicate a higher observed proportion in the first-named comparison arm; negative values indicate a lower observed proportion. These are descriptive directions, not proof that assignment caused a difference.

What does the confidence interval describe?

A confidence interval represents uncertainty around an estimated contrast under the statistical method used to construct it. In general, a wider interval indicates less precision. For these recalculated risk differences, each primary-outcome interval includes zero, the value corresponding to no difference in the proportions. That means the posted data are compatible with a range of possible differences on either side of zero. The interval is not a range containing a known fixed share of individual participant outcomes, and it does not remove uncertainty about the measurement or design.

How should the p-values be read?

The p-values shown with the recalculated comparisons are unadjusted. In general, a p-value measures how unusual data at least as incompatible with a null hypothesis would be under that hypothesis and the assumed statistical model. It is not the probability that the null hypothesis is true, nor does it measure the size or practical importance of an effect. Interpretation should consider the estimated difference and its confidence interval, not a threshold alone. The registry does not report its own analyses for these outcomes or an analysis plan that would clarify which tests were prespecified.

Why use an unadjusted risk difference?

The endpoint is binary at the participant level: a participant either contributes to the count of infants usually sleeping supine or does not. A risk difference gives an absolute contrast on the proportion scale, which is often straightforward to interpret. The posted results also include risk-ratio and odds-ratio summaries, but those are alternative scales for describing the same comparison. None should be read as an adjusted estimate because the recalculations use posted arm-level summary statistics.

What do the denominator differences mean?

For the primary endpoint, each arm’s denominator is the number of participants who provided information about infant sleep position. Secondary endpoints have their own arm-specific denominators. Different denominators can reflect differing availability of outcome information, but the reason for each difference and the handling of missing observations are not reported in the registry record. It is therefore not possible to determine from these summaries whether missingness was related to assignment or outcome, or how any missing information was treated in the trial’s own analyses.

What does the design label tell us?

The registry calls the trial randomized, single-masked, and sequential. Randomization supports comparisons among assigned groups, in general, by reducing systematic baseline differences on average when implemented as intended. The record does not specify sequence generation, concealment, who was masked, or what sequential means operationally. No claim about these procedures should be inferred from the labels alone. Details of the original statistical plan, covariate adjustment, interim analyses, or sample-size justification are not reported in the registry record.

Because the registry lists no reported analyses, the presented contrasts should be understood as unadjusted recalculations, not as a substitute for a trial analysis that may use additional data or account for design features. The discrepancy indicator is false, so no disagreement with a sponsor-reported estimate is flagged in this record. Even so, the absence of a reported analysis leaves the intended inferential approach unclear.

11. Confidence Intervals and Precision

Precision is reflected in the width of a confidence interval, not only in the point estimate. The primary comparison for prenatal safe-sleep/postnatal breastfeeding messaging has a risk-difference interval from -0.034 to 0.049. The prenatal breastfeeding/postnatal safe-sleep comparison has an interval from -0.063 to 0.026, and the breastfeeding-message combination in both periods has an interval from -0.083 to 0.008. Each includes zero, so the data do not tightly pin down the direction of the primary-outcome contrast.

In general, a confidence interval describes a range of values reasonably compatible with the observed data under the method’s assumptions. Its width is influenced by the amount of information and the variability of the outcome. Here, the primary outcome is binary, and the number analyzed in each arm is based on participants who reported infant sleep position. The intervals therefore reflect sampling uncertainty under the recalculation method, but they do not capture possible reporting error, bias from missing outcome information, or uncertainty about unreported design procedures.

The estimates are not evidence that the true difference is exactly zero. Rather, the interval includes both zero and values on either side, so the summaries leave room for more than one interpretation. A point estimate near zero does not by itself show equivalence; an equivalence conclusion would require a defined margin and an appropriate analysis, neither of which is reported in the registry record. Likewise, an interval crossing zero does not establish that the compared message combinations have identical effects.

The intervals also apply only to the specified pairwise comparisons and outcome definition. They do not describe the full range of individual responses, and they should not be transferred to exclusive supine sleep, room sharing, or breastfeeding outcomes. The registry lists no reported analyses, so these intervals belong to the simple recalculations from posted summary counts rather than a documented sponsor analysis.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations show participants per arm for 80% power and participants per arm for 90% power. They are not totals across arms or total event counts. The planning 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 the stated fraction of the observed effect. The original trial design assumptions and sample-size justification are not reported in the registry record.

In general, power is the chance that a study will detect an effect of a specified size under the assumptions used for planning, if that effect is present. The 80% and 90% columns describe two planning targets: the participant count per arm estimated to reach each target under the stated assumptions. A higher target generally requires more participants for the same assumed effect. Each planning row scales the observed effect to a stated fraction. Smaller effects need more participants to detect than larger effects, all else held constant.

These calculations use the observed effect as their starting point, rather than a separately justified target difference. That makes them illustrations of planning under stated assumptions, not evidence about the study’s original design choices. They do not account for unreported features such as missing outcome data, departures from equal allocation, or any design adjustments. The registry labels the sample-size assumptions as a planning illustration computed from the observed effect. This is not observed power; it should not be used to characterize how likely the completed trial was to detect its results.

The table and curve should be read as planning aids for hypothetical future comparisons, not as a retrospective verdict on the trial. Because the trial’s own design assumptions are not reported in the registry record, these illustrations cannot establish whether the enrollment was chosen to answer the primary question with a particular precision.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.914; treatment proportion p₁ = 0.922; average p̄ = 0.918.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3886 = 0.7616.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3886 = 0.3270.
4. n = (0.7616 + 0.3270)² / (0.0076)² = 20,708.6, rounded up to 20,709 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 <- 0.913946587537092                          # control proportion
p1 <- 0.921511627906977                          # 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(4387552)
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 = 20,709 (80% power), 27,723 (90% power)
 75% of observed effect: n per arm = 37,202 (80% power), 49,802 (90% power)
 50% of observed effect: n per arm = 84,568 (80% power), 113,212 (90% power)
power.prop.test: 20708.6 
Simulated power at n = 20,709 per arm: 0.804 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists three secondary outcomes and eight outcome measures overall, but it does not report the analysis plan for controlling multiplicity. Multiplicity arises when several outcomes or comparisons are tested: even if no real differences exist, examining many results can make an apparently unusual result more likely to occur by chance. Common approaches include adjusting the threshold for inference or specifying a hierarchy of outcomes in advance. Whether either approach was used is not reported in the registry record. The posted secondary comparisons are unadjusted, so they should be interpreted cautiously, especially when one comparison appears more notable than the broader pattern.

The registry lists no reported analyses for the primary or secondary results. It therefore does not establish which outcomes or contrasts were prespecified for formal testing, whether the pairwise comparisons were planned, or whether covariate adjustment was intended. The registry record also does not report interim analyses or a statistical analysis plan. These omissions limit the ability to distinguish confirmatory analyses from exploratory ones.

Outcome-specific denominators show that not every arm has the same number of participants contributing information to every measure. The primary endpoint definition says that the analyzed number in each arm reflects participants who provided information about infant sleep position. The reasons for absent information, its timing, and its handling are not reported. There is no basis to assume that missing data were random, or to infer that a particular imputation, exclusion, or sensitivity analysis was used.

The analysis populations are also not described in detail. The record does not state whether analyses followed intention-to-treat principles, whether participants were analyzed according to assignment, or whether any per-protocol population was used. Enrollment is listed as 2093, but that figure does not explain which participants contributed to each endpoint analysis. The arm-level outcome denominators should therefore be read as the numbers with information for those measures, not as a complete account of all randomized participants or of the analysis population definition.

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 5% reporting threshold.

The registry reports zero serious adverse events and zero other adverse events in each of the four arms. For serious events, the at-risk counts listed are 346 for prenatal and postnatal safe-sleep messaging, 350 for prenatal safe-sleep/postnatal breastfeeding messaging, 338 for prenatal breastfeeding/postnatal safe-sleep messaging, and 349 for breastfeeding messaging in both periods. The other-adverse-event at-risk counts are the same as those listed for serious events in each arm. Deaths are reported as zero in every arm.

These figures describe what the registry reports during its safety reporting period; they do not establish that no events occurred outside that period or were not captured. The record does not give a safety observation timeframe, event definitions, methods of ascertainment, or a detailed account of reporting completeness. Zero recorded events should therefore be read as zero events reported in these registry results, not as proof of absence of risk. The study interventions are classified as behavioral, but that classification alone does not determine how safety was monitored.

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

The posted primary results describe the proportions of participants reporting that their infants usually slept supine during the previous two weeks across four combinations of prenatal and postnatal mobile messages. The recalculated point estimates are close to zero on the risk-difference scale, and all three confidence intervals include zero. These summaries do not provide a precise basis for distinguishing the compared combinations on this endpoint.

That interpretation is narrower than saying that the messages did or did not work. A nonzero point estimate can occur through sampling variation, and an interval that includes zero does not establish equivalence. Conversely, the posted estimates do not demonstrate a clear difference. The registry lists no sponsor-reported analyses for these outcomes, and the available calculations use arm-level summary counts without adjustment for other factors.

The outcome is a maternal survey report of usual position over a recall period. It does not directly measure adherence throughout all sleep episodes, actual message exposure, or clinical outcomes such as SUID or SIDS. The registry lists those conditions, but the results concern reported sleep and feeding practices. No inference about changes in clinical event rates should be drawn from these behavioral outcome counts.

Each arm combines two message periods, so the pairwise contrasts do not isolate prenatal content from postnatal content. The record does not report analyses separating those components. Secondary outcomes provide additional but mixed information, and their unadjusted nature means isolated findings warrant caution. Missing-data handling, the analysis population, and the original statistical plan are not reported, limiting assessment of possible bias and the intended inferential framework.

The practical meaning is therefore that the registry’s posted summaries offer an uncertain comparison of reported practices under the assigned message combinations. They do not establish that one combination is superior, that the combinations are equivalent, or that any finding applies beyond the measured outcomes and assessment period.

17. Why This Trial Matters Statistically

This trial illustrates a common challenge in behavioral intervention research: assignment can vary across more than one period, while the outcomes depend on participant report. The four combinations make the comparison more informative than a simple message-versus-no-message contrast in some respects, but the registry does not report a factorial analysis that separates prenatal and postnatal components. The posted pairwise contrasts therefore answer narrower questions about combinations rather than identifying which message period accounts for any difference.

It also highlights the distinction between an endpoint count and the number enrolled. The primary endpoint denominator includes participants who provided sleep-position information, and denominators vary across outcomes. This matters because precision and interpretation depend on the data available for the specific measure. Without the missing-data methods and analysis-population definitions, the endpoint-specific counts cannot reveal whether information availability influenced the comparisons.

The results emphasize why effect estimates and confidence intervals should be considered together. The primary estimates are not precise enough to exclude zero, and the intervals allow differences in either direction. A p-value alone cannot answer whether an effect is important, whether a result is robust to analytic choices, or whether the estimate is sufficiently precise for a decision. The lack of reported analyses and multiplicity procedures further limits claims based on individual comparisons.

Finally, the sample-size illustrations show how planning depends on the effect a future study aims to detect, but they are based on observed effects rather than the trial’s documented original assumptions. They are planning aids, not evidence of the trial’s design adequacy. Taken together, this record is a useful example of how registry summaries can describe outcomes while leaving important questions about analysis plans, missing information, and interpretation unresolved.

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.

Several limitations are specific to the information available for this trial. First, the primary outcome is based on an investigator-developed maternal survey. The registry does not report validation information, response rates, or procedures for checking reported sleep position. Recall and reporting differences could affect the measurement, but their magnitude cannot be determined from the record.

Second, the assessment timing is described as between 2 and 6 months following postnatal randomization, on average 67.7 days. The registry does not explain variation in timing or report whether timing was balanced across arms. The outcome refers to the previous two weeks, so the result represents a limited recall window rather than continuous behavior over the follow-up period.

Third, the reported denominators vary by outcome and arm. The record does not describe reasons for missing information, how missing outcomes were handled, or whether missingness differed by assignment. Without those details, it is difficult to assess potential selection effects in the analyzed participants. The analysis populations are not defined, and the registry lists no reported analyses.

Fourth, the trial combines prenatal and postnatal message topics across four arms. Although the posted pairwise contrasts compare combinations, the registry does not report estimates that isolate the effect of either period or describe the sequential model in operational terms. The masking label is also not accompanied by information about who was masked.

Finally, the registry does not report the protocol-level statistical plan, multiplicity handling, interim analyses, or the original sample-size justification. The unadjusted recalculations and planning illustrations cannot fill those gaps. These limitations constrain both causal interpretation and the ability to evaluate how the posted comparisons relate to the study’s intended analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Social Media and Risk Reduction Teaching-Enhanced Reach — NCT04387552.
• Registry record last updated 2026-08-26; status last verified 2026-08.
• Results first posted 2026-08-26.
• 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

NCT04387552 is a completed randomized study sponsored by Boston University, listed as single-masked and sequential. It evaluates prenatal and postnatal mobile health messaging about safe sleep and breastfeeding. The primary outcome is the number of participants reporting usual infant supine sleep during the previous two weeks, assessed between 2 and 6 months following postnatal randomization, on average 67.7 days.

The posted primary comparisons are unadjusted recalculations from arm-level counts. Their risk-difference confidence intervals all include zero. Secondary outcomes cover exclusive supine sleep, room sharing without bedsharing, and exclusive breastmilk feeding; the pattern across their unadjusted comparisons is mixed. The registry lists no reported analyses and does not report the analysis plan, missing-data handling, or multiplicity procedures. Safety results list zero serious adverse events, zero other adverse events, and zero deaths in each arm.