A Trial of AI-Powered Text Message Outreach on Well-Child Visit Completion: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Trial of AI-Powered Text Message Outreach on Well-Child Visit Completion (NCT06698640), a randomized na study. The primary outcome is Number of Participants With Well-Child Visit Completion.

2. Clinical Question

The clinical question concerns both the effect of reminders and the additional contribution of concrete scheduling support. The three groups make it possible to distinguish the reminder-only strategy from the strategy that adds assistance with arranging an appointment. The primary endpoint was an indicator of whether a participant completed at least one well-child visit by December 31, 2025, based on administrative claims and HEDIS technical specifications.

The registry describes the trial as testing preventive-care utilization in pediatric Medicaid populations. Its outcome is visit completion recorded in claims, not a measure of health status, quality of the visit, or the reason a visit was or was not completed. The findings therefore address the recorded completion outcome for the trial population and outreach strategies, rather than every aspect of access to or receipt of preventive care.

3. Trial Design

The registry describes a randomized, double-blind, parallel, three-arm trial with enrollment of 2821. Randomization was at the household level. The arms were traditional passive outreach, automated SMS reminders, and automated SMS with conversational AI scheduling assistance. The record labels the phase as NA and the study status as completed.

Participants received outreach from June 9-July 14, 2025. Well-child visit completion was ascertained through administrative claims through December 31, 2025. The primary endpoint timeframe is described as up to 7 months post-randomization, with the record also giving June 1 - December 31, 2025. The registry identifies Waymark as the sponsor.

In the control arm, families received periodic mailed reminders and retained access to standard appointment scheduling methods. The automated SMS arm received standardized reminders at predetermined intervals, with instructions to contact providers to schedule. The combined arm added a response pathway to collect appointment preferences and AI-powered assistance contacting primary care providers to arrange appointments. The registry’s arm descriptions are not complete in all details, so the full operational procedures are not reported in the registry record.

Although assignment was at the household level, the primary endpoint and posted results are described for participants. Whether the analysis accounted for correlation among participants from the same household, and the precise analysis population for each reported comparison, are not reported in the registry record. The record identifies double masking but does not specify which people were masked or how masking was maintained.

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: Only Medicaid-enrolled children aged 0-21 years were enrolled. Parents/caregivers who received texts or interacted with the AI scheduler on behalf of children were not enrolled; no parent/caregiver data were collected and they are not represented in Baseline Characteristics, Outcome Measures, or Adverse Events. Randomization was conducted at the household level on June 1, 2025, in a 1:1:1 ratio.

Overall Study

Analysis population for the primary outcome, as defined in the registry: All randomized participants with available claims data through December 31, 2025 (intent-to-treat population). Participants with no claims data were assumed to have not completed a well-child visit.

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: Participants with an open well-child visit gap, defined as no completed well-child visit in the prior measurement year per HEDIS technical specifications. An open gap at baseline was an eligibility criterion; therefore 100% of randomized participants met this criterion.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Well-Child Visit Completion, measured over Up to 7 months post-randomization (June 1 - December 31, 2025).

The primary endpoint is the number of participants with well-child visit completion. It represents a binary outcome for each participant: whether at least one well-child visit was completed by December 31, 2025. Completion was ascertained from administrative claims using HEDIS technical specifications. The outcome is therefore a count of participants meeting the completion definition, rather than a count of visits.

This endpoint is used because the trial asks whether outreach strategies change completion of a preventive-care visit. A binary completion measure provides a direct basis for comparing the proportion of participants with a recorded visit across randomized groups. It captures whether the specified threshold was reached, but does not distinguish participants with one visit from those with more than one, describe the content or quality of a visit, or establish why a participant did not have a visit recorded.

The registry defines the primary analysis population as all randomized participants with available claims data through December 31, 2025. Participants with no claims data were assumed not to have completed a well-child visit. That rule makes the treatment of absent claims explicit, but does not by itself establish whether all participants had equivalent claims coverage or whether any missing claims reflected no visit. The amount of missing claims data and any sensitivity analyses for that assumption are not reported in the registry record.

The endpoint is relevant to the stated question about care completion, while remaining a claims-based measure of documented utilization. It does not directly measure health benefit or the broader experience of families trying to obtain care.

7. Results Posted in the Registry

• Automated SMS: 22.0% (209/949) versus 23.5% (218/927) on control; risk difference -1.5 percentage points (95% CI -5.3 to 2.3), risk ratio 0.94 (0.79–1.11); unadjusted two-proportion z-test p = 0.440.
• Automated SMS + Scheduling Assistance: 29.6% (280/945) versus 23.5% (218/927) on control; risk difference 6.1 percentage points (95% CI 2.1 to 10.1), risk ratio 1.26 (1.08–1.47); unadjusted two-proportion z-test p = 0.003.

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.

Staff Time Per Successfully Scheduled Appointment

• 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:
  • Automated SMS + Scheduling Assistance: mean 2.00 versus 14.00 on control; difference -12.00 (95% CI -12.84 to -11.16), standardized effect d = -3.66; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Automated SMS + Scheduling Assistance than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the trial’s focus from whether a well-child visit was completed to operational aspects of scheduling. The registry names staff time per successfully scheduled appointment and the human escalation rate for automated scheduling attempts. The posted secondary evidence indicates a pattern in which the scheduling-assistance strategy is associated with lower staff time, alongside the primary-outcome pattern in which the sponsor reports a difference between the two SMS groups.

These outcomes address different parts of the intervention pathway. Visit completion is a utilization outcome, while staff time and escalation concern the process of arranging appointments. Taken together, the types of outcomes can help distinguish whether a scheduling service is associated with both completion and operational workload. They do not establish that one process caused the other, and they should not be treated as independent confirmation of the primary result.

The registry does not report results for the human escalation rate in the posted secondary analyses. The amount and detail of secondary-outcome information are therefore limited. The staff-time analysis is reported as a time-motion analysis, but the registry does not describe its sampling procedures or all relevant operational definitions.

Secondary findings generally carry less weight than a prespecified primary endpoint because they may involve additional comparisons and greater scope for chance findings. The registry record does not report whether secondary analyses were prespecified in a statistical analysis plan, whether multiplicity was controlled, or how missing secondary data were handled. Without those details, the secondary findings are best viewed as supporting operational evidence rather than as standalone confirmatory tests.

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

• Staff Time Per Successfully Scheduled Appointment
• Human Escalation Rate for Automated Scheduling Attempts

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical measures appear in the registry record. They answer related but different questions, and estimates should be read alongside their confidence intervals and the analysis description.

What does a risk difference express?

General: a risk difference compares the event proportions in two groups by subtracting one group’s proportion from the other. It is expressed on the probability scale, so a positive value means a higher event proportion in the group named first in the contrast, while a negative value means a lower proportion. A confidence interval gives a range of values compatible with the data under the analysis assumptions. If the interval includes zero, the data do not clearly distinguish the contrast from no difference at the confidence level used.

The record reports a risk difference of -1.5, with a 95% confidence interval from -5.3 to 2.3 and p = 0.44, for Control versus Automated SMS. The interval includes zero, consistent with the reported p-value not indicating a clear difference in that comparison. For Automated SMS + Scheduling Assistance versus Automated SMS, the sponsor reports a risk difference of 7.6, with a 95% confidence interval from 3.7 to 11.5 and p < .001. That interval is entirely above zero. The reported values are retained as recorded; the registry’s analysis definition and adjustments are not fully described.

How does an odds ratio differ?

General: an odds ratio compares odds rather than event probabilities. Odds and probabilities are related, but they are not the same scale. An odds ratio of 1 represents equal odds under the stated contrast; values above or below 1 indicate higher or lower odds, respectively. It should not be read as a risk difference or as a direct percentage-point change.

The registry reports a GEE odds ratio of 1.60, with a 95% confidence interval from 1.28 to 2.01 and p < .001, for the three groups together. The record identifies GEE as the method, but does not report the model specification, coding of group effects, covariates, or the precise interpretation of the single odds ratio across the three groups. It is therefore best read as a reported overall modeled association, not as a substitute for the pairwise risk differences.

What does a chi-squared test assess?

General: a chi-squared test can assess whether categorical outcome distributions differ across groups. Its p-value summarizes how unusual the observed pattern would be under the test’s null hypothesis and assumptions. It does not state the size of a difference, show which pair of groups differs, or measure the probability that the null hypothesis is true.

The registry reports an overall chi-squared p < 0.001 for the three groups. It also reports pairwise chi-squared analyses with risk differences. The overall result indicates evidence of a difference somewhere in the three-group comparison under that test; it does not, by itself, identify the particular pair responsible or quantify the clinical scale of the difference.

Why can household assignment matter?

General: when randomization occurs by household, outcomes from people in the same household may be correlated. Analyses that treat every participant as fully independent can understate uncertainty if that correlation is not handled appropriately. Methods such as GEE can account for correlated observations when specified to do so, but the method’s label alone does not reveal which clustering structure or variance approach was used.

The record states that households were randomized and reports a GEE analysis, but it does not say whether household was the clustering unit in that model or explain how clustering was handled in the pairwise analyses. This is an important reporting gap for interpreting uncertainty, not grounds for assuming that the analysis was or was not correctly adjusted.

What is the role of unadjusted re-calculation?

The re-calculated risk differences and confidence intervals are simple, unadjusted comparisons based on the posted group summaries. They provide a transparent descriptive comparison, but they may not match the sponsor’s analysis if the sponsor used a different model, analysis population, treatment of clustering, or other specifications. The registry flags a discrepancy, so the sponsor’s own analysis takes precedence. The registry record does not report the full statistical analysis plan, model specifications, or all details needed to reproduce the sponsor’s analyses.

11. Confidence Intervals and Precision

A confidence interval describes the range of effect estimates that are reasonably compatible with the observed data under the analysis assumptions. Its width conveys precision: a narrower interval indicates less statistical uncertainty than a wider interval on the same scale. A confidence interval is not a guarantee that the true effect lies inside it, and it does not account for unreported sources of bias or model misspecification.

For Control versus Automated SMS, the sponsor reports a risk difference of -1.5 with a 95% confidence interval from -5.3 to 2.3. Because that interval crosses zero, the data do not clearly distinguish the comparison from no difference at the stated confidence level. The associated p-value is 0.44. This is not proof that the strategies are identical; the interval still includes values on either side of zero.

For Automated SMS + Scheduling Assistance versus Automated SMS, the sponsor reports a risk difference of 7.6 with a 95% confidence interval from 3.7 to 11.5. The interval lies above zero, and the reported p-value is < .001. For the overall GEE result, the odds ratio is 1.60 with a 95% confidence interval from 1.28 to 2.01. This interval lies above the odds-ratio null value of 1. These sponsor-reported intervals support the reported evidence of differences, but their interpretation depends on the analyses and assumptions that are not fully described in the registry record.

The unadjusted re-calculation comparing Automated SMS + Scheduling Assistance with Control has a risk difference of 0.061 and a 95% confidence interval from 0.021 to 0.101. That is a separate contrast and should not be substituted for the sponsor’s pairwise SMS comparison. The registry record flags a discrepancy, so the sponsor’s analysis takes precedence. Confidence intervals quantify sampling uncertainty under a model; they do not resolve questions about missing claims, clustering, or generalizability.

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 illustrations use the observed effect as a reference and show the participants per arm needed under stated hypothetical assumptions. For the primary binary endpoint and the continuous staff-time outcome, the figures are participants per arm, not total events. The registry’s general convention is that time-to-event calculations would give total events, but no time-to-event outcome is described among these results.

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 set to the stated fraction of the observed effect. The registry record does not report the trial’s original design assumptions or sample-size justification, so these illustrations should not be read as the plan used to design or conduct the trial.

The 80% power column represents a hypothetical participant count per arm intended to give an 80% chance of detecting the chosen effect under those assumptions if that effect were the true effect. The 90% power column uses a higher target chance of detection, which generally requires more participants per arm for the same effect. These are planning illustrations, not observed power.

Smaller effects are harder to distinguish from random variation, so detecting a smaller fraction of the observed effect requires more participants per arm. For example, the rows labeled 75% of the observed effect and 50% of the observed effect represent progressively smaller target effects than the row using 100% of the observed effect. The resulting figures are scenarios, not evidence that the trial was adequately or inadequately powered for its original aims.

The planning values are also sensitive to the assumptions behind them. Equal allocation, the normal approximation, and the assumed effect size may not reflect every feature of a future study. In particular, the registry record does not report how the household-level randomization was incorporated into these planning calculations. The original design assumptions are 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.235; treatment proportion p₁ = 0.220; average p̄ = 0.228.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5930 = 1.1624.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5930 = 0.4990.
4. n = (1.1624 + 0.4990)² / (-0.0149)² = 12,374.1, rounded up to 12,375 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 <- 0.235167206040992                          # control proportion
p1 <- 0.220231822971549                          # 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(6698640)
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 = 12,375 (80% power), 16,565 (90% power)
 75% of observed effect: n per arm = 22,126 (80% power), 29,620 (90% power)
 50% of observed effect: n per arm = 50,069 (80% power), 67,027 (90% power)
power.prop.test: 12374.1 
Simulated power at n = 12,375 per arm: 0.798 (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. Analyses Reported by the Sponsor

The registry contains sponsor-reported analyses as well as simple unadjusted re-calculations from the posted group summaries. The sponsor reports a risk difference of 7.6, with a 95% confidence interval from 3.7 to 11.5 and p < .001, for Automated SMS + Scheduling Assistance versus Automated SMS. The sponsor also reports a risk difference of -1.5, with a 95% confidence interval from -5.3 to 2.3 and p = 0.44, for Control versus Automated SMS. An overall chi-squared analysis has p < 0.001, and a GEE analysis reports an odds ratio of 1.60, with a 95% confidence interval from 1.28 to 2.01 and p < .001.

The simple re-calculations are based on the posted arm summaries and are unadjusted. They include a contrast of Automated SMS + Scheduling Assistance with Control, whereas the sponsor’s pairwise comparison of the two SMS groups addresses a different question. The GEE odds ratio is also on a different scale and is reported across the three groups. Differences between these results can reflect differences in contrast, model, analysis population, or handling of household assignment; the registry record does not provide enough detail to determine the explanation.

The registry marks a discrepancy between the sponsor analysis and re-calculation. Accordingly, the sponsor’s own analysis takes precedence. Re-calculations are useful as checks on the posted counts, but should not be presented as replacements for the sponsor’s analysis or as a reconstruction of its statistical model.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is clearly identified, but the registry record does not report a complete statistical analysis plan. It does not describe whether the three-arm overall test was followed by a prespecified sequence of pairwise comparisons, whether the pairwise tests were adjusted for multiplicity, or whether any hierarchy governed interpretation. When several comparisons or outcomes are examined, the chance of at least one apparently unusual result can increase. General statistical practice may address this through prespecified testing strategies or adjustments, but whether either was used is not reported in the registry record.

The primary population is described as all randomized participants with available claims data through December 31, 2025, with participants lacking claims assumed not to have completed a visit. This is an explicit outcome rule, but the record does not report how many participants lacked claims, whether missingness differed by group, or whether sensitivity analyses explored alternative assumptions. The extent of missing outcome data therefore cannot be assessed from the registry record.

Household-level randomization creates a potential dependence among participants assigned together. The registry does not report whether analyses accounted for household clustering, how the GEE was specified, or whether the pairwise tests incorporated the randomization unit. This limits assessment of the reported standard errors and confidence intervals.

The record does not report interim analyses, stopping rules, covariate adjustment details, or the full analysis population for every comparison. It also does not describe how deviations from the intended outreach or incomplete intervention delivery were handled. These omissions do not establish that the analyses were inappropriate, but they limit independent appraisal of the statistical procedures and the robustness of the reported results.

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

The posted results describe differences in claims-recorded well-child visit completion across the trial’s outreach strategies. The sponsor reports a difference between Automated SMS + Scheduling Assistance and Automated SMS, while its Control-versus-Automated-SMS comparison does not show clear evidence of a difference. The overall chi-squared and GEE results also indicate differences across groups under the reported analyses. These findings concern the endpoint and population defined in the registry record.

The outcome is not a direct measure of health improvement, quality of care, family satisfaction, or whether a missed visit was clinically important. A claim-based completion indicator records whether at least one qualifying visit was identified under the stated approach. It cannot by itself explain why completion differed, show whether the service was equally accessible to all families, or identify which elements of the combined intervention were responsible for the pattern.

The comparison between the two SMS arms is informative about adding scheduling assistance to reminders, but it does not isolate every feature of that assistance. The intervention includes a response process, collection of appointment preferences, and contact with providers. The registry record does not report component-level analyses that would separate their contributions.

The findings should not be generalized automatically beyond Medicaid-enrolled children aged 0-21 years in this trial, the outreach procedures used, and the claims-based outcome window. The record does not provide information about settings or populations beyond the stated trial population. Nor do the results establish that the same effects would occur with different messaging systems, appointment availability, or implementation arrangements.

Finally, a statistically notable result is not by itself a complete judgment about practical importance. The sponsor-reported estimates and their uncertainty describe the recorded comparisons, while the limitations in analysis reporting and missing-data detail remain relevant to how confidently the results can be interpreted.

17. Why This Trial Matters Statistically

This trial is statistically useful because its three-arm structure separates passive mailed outreach, automated reminders, and reminders paired with scheduling assistance. That design addresses a practical analytic distinction: whether communication alone is associated with a different completion outcome, and whether adding help with appointment arrangement is associated with a further difference.

The comparison also illustrates why the contrast must be named precisely. A result for Automated SMS versus Control answers a different question from Automated SMS + Scheduling Assistance versus Automated SMS. An overall test across all groups asks whether the pattern differs somewhere, while a pairwise contrast estimates a particular group difference. The GEE odds ratio is on a different scale from the risk differences. Treating these outputs as interchangeable would obscure what each analysis estimates.

The record also illustrates the role of uncertainty and analysis transparency. Confidence intervals show the precision of estimates under their assumptions, while missing details about household clustering, multiplicity, and the sponsor model limit how fully an outside reader can assess the analyses. The discrepancy flag reinforces the importance of distinguishing descriptive re-calculation from the sponsor’s own reported analysis.

Finally, the trial pairs a clinical-utilization endpoint with operational secondary outcomes. That combination can inform statistical thinking about how intervention processes and patient-level outcomes relate, without implying that one necessarily explains the other. It highlights why endpoint definitions, analysis populations, and the unit of randomization should all be considered when interpreting a trial’s results.

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 provides only partial operational descriptions for the outreach arms. The descriptions establish the broad distinction between mailed reminders, standardized text reminders, and text reminders with AI scheduling assistance, but some details are incomplete. The registry record does not report all implementation procedures, adherence measures, or how often families engaged with each intervention component.

Households were randomized, while the primary outcome is described at the participant level. The registry does not state how household clustering was handled in each analysis. This leaves uncertainty about whether the reported estimates and precision fully reflect the assignment structure. The record identifies a GEE analysis but does not supply enough model detail to resolve that issue.

Claims-based ascertainment and the assumption that participants with no claims data had no completed visit are additional limitations. The registry does not report the amount of missing claims information, group-specific missingness, or sensitivity analyses. Claims-based recording may not capture every relevant detail of care, and the endpoint does not measure visit quality or health outcomes.

The registry also reports a discrepancy between the sponsor’s analysis and the unadjusted re-calculations. Because the full analysis specifications are not reported, the reason for that discrepancy cannot be established from the record. Details about multiplicity control, interim analyses, sample-size justification, and the handling of deviations from assigned outreach are also not reported in the registry record.

Safety fields list zero events in the groups, but the corresponding at-risk fields are also zero. Those entries do not establish that no adverse events occurred; the safety information is not interpretable as a complete assessment of event occurrence from the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Trial of AI-Powered Text Message Outreach on Well-Child Visit Completion — NCT06698640.
• Registry record last updated 2026-10-16; status last verified 2026-09.
• Results first posted 2026-06-22.
• 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

NCT06698640, titled “A Trial of AI-Powered Text Message Outreach on Well-Child Visit Completion,” is a completed randomized, double-blind, parallel, three-arm trial sponsored by Waymark. The registry lists enrollment of 2821 and household-level randomization. The groups received traditional passive mailed outreach, automated SMS reminders, or automated SMS with conversational AI scheduling assistance.

The primary outcome was the number of participants completing at least one well-child visit by December 31, 2025, ascertained from administrative claims using HEDIS technical specifications. The registry reports an overall chi-squared p < 0.001, pairwise risk-difference analyses, and a GEE odds ratio. It also lists secondary operational outcomes concerning staff time and human escalation.

The record flags a discrepancy between sponsor analyses and unadjusted re-calculations; the sponsor’s own analysis takes precedence. Details on multiplicity, household-cluster handling, missing claims, and the full statistical analysis plan are not reported in the registry record.