Effect of Varied Outreach Methods on Appointment Scheduling, Appointment Completion, and Receipt of MMR Vaccination: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of Varied Outreach Methods on Appointment Scheduling, Appointment Completion, and Receipt of MMR Vaccination (NCT04567342), a randomized na study. The primary outcome is Receipt of MMR Vaccination.

2. Clinical Question

3. Trial Design

This was a randomized, single-masked, factorial trial with four arms. The record lists enrollment as 1312 and status as completed. It identifies Children’s Hospital Medical Center, Cincinnati as sponsor. The study dates in the registry record are 2020-11-27 for the start and 2021-08-06 for primary completion. Phase is listed as NA.

The study concerned children age 12-14 months or 4 years old who were due for a well-child care visit and did not have one scheduled in the next 45 days. The stated objective was to assess varied outreach methods, including automated reminders and personalized contact, in relation to scheduling, completing an appointment, and receipt of MMR vaccination. Four intervention labels appear in the record: 1 automated message, 2 automated messages, no personal contact attempt, and 1 personal contact attempt. The arm descriptions themselves are blank, so assignment of those labels to specific arms is not reported in the registry record.

For the primary outcome, Arm 1 included 329.0 participants, Arm 2 included 328.0, Arm 3 included 328.0, and Arm 4 included 327.0. These arm-specific denominators describe the posted primary outcome counts. The record identifies the allocation as randomized and masking as single, but does not report which parties were masked or how randomization was generated or implemented.

The factorial designation indicates a design structured around more than one intervention component, but the factorial factors, their levels, and the planned contrasts are not described in the registry record. The original protocol, design assumptions, analysis population, and statistical analysis plan are not reported in the registry record. Therefore, the posted arm comparisons can be described, but their relation to any intended factorial main effects or interactions cannot be established from the record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

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 Receipt of MMR Vaccination, measured over By 15 months of age (for children who are 12-14 months old), or within 3 months of receiving intervention (for children age 4 years old).

The primary endpoint is receipt of MMR vaccination, recorded as whether a participant received the vaccine. The registry describes the measure as MMR administered to the child, yes or no, based on electronic health record documentation. It is a binary outcome: each participant contributes either a recorded vaccination event or no recorded event for the assessment.

The outcome is assessed on different schedules according to the children’s age group. For children who were 12-14 months old, the timeframe is by 15 months of age. For children age 4 years old, the timeframe is within 3 months of receiving the intervention. These timeframes are part of the endpoint definition and should be kept in mind when interpreting the pooled arm summaries; subgroup-specific outcome results are not reported in the registry record.

Using a documented vaccination as the primary measure connects the outcome to a concrete service received, rather than relying solely on a stated intention or appointment booking. At the same time, an electronic health record measure reflects recorded documentation. The registry record does not describe how records outside the system were handled, how missing documentation was classified, or whether vaccination was verified by any other source. The endpoint therefore represents documented receipt under the registry’s stated measure, not necessarily every vaccination that may have occurred.

The trial also reported appointment scheduling within 2 weeks and appointment completion within 8 weeks as secondary outcomes. Those measures capture earlier steps in the care pathway, while the primary outcome concerns documented MMR receipt over its stated age-specific timeframe.

7. Results Posted in the Registry

• Arm 2: 23.5% (77/328) versus 28.0% (92/329) on control; risk difference -4.5 percentage points (95% CI -11.2 to 2.2), risk ratio 0.84 (0.65–1.09); unadjusted two-proportion z-test p = 0.188.
• Arm 3: 30.2% (99/328) versus 28.0% (92/329) on control; risk difference 2.2 percentage points (95% CI -4.7 to 9.2), risk ratio 1.08 (0.85–1.37); unadjusted two-proportion z-test p = 0.531.
• Arm 4: 31.8% (104/327) versus 28.0% (92/329) on control; risk difference 3.8 percentage points (95% CI -3.2 to 10.8), risk ratio 1.14 (0.90–1.44); unadjusted two-proportion z-test p = 0.283.

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.

Appointment Scheduled

• 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:
  • Arm 2: 12.5% (41/328) versus 15.2% (50/329) on control; risk difference -2.7 percentage points (95% CI -8.0 to 2.6), risk ratio 0.82 (0.56–1.21); unadjusted two-proportion z-test p = 0.317.
  • Arm 3: 29.3% (96/328) versus 15.2% (50/329) on control; risk difference 14.1 percentage points (95% CI 7.8 to 20.3), risk ratio 1.93 (1.42–2.61); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 2 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 higher for Arm 3 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Appointment Completed

• 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:
  • Arm 2: 22.3% (73/328) versus 27.4% (90/329) on control; risk difference -5.1 percentage points (95% CI -11.7 to 1.5), risk ratio 0.81 (0.62–1.06); unadjusted two-proportion z-test p = 0.130.
  • Arm 3: 32.0% (105/328) versus 27.4% (90/329) on control; risk difference 4.7 percentage points (95% CI -2.3 to 11.6), risk ratio 1.17 (0.92–1.48); unadjusted two-proportion z-test p = 0.191.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 2 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 Arm 3 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes follow steps that precede or accompany documented vaccination: appointment scheduling within 2 weeks of receiving the intervention and appointment completion within 8 weeks. Across these measures, the posted results suggest that the outreach arms did not all have identical event patterns. The clearest statistical signal in the sponsor’s reported secondary analyses is for scheduling in one comparison with Arm 1; the completion comparisons do not show a similarly clear pattern. This contrast in evidential strength does not establish that a change in scheduling led to a change in vaccination receipt.

The primary endpoint remains the measure of documented MMR receipt. Its sponsor-reported Arm 1 comparisons do not provide clear statistical evidence of differences, so the secondary scheduling signal should be viewed as a process finding rather than confirmation of a primary outcome effect. Appointment scheduling, appointment completion, and vaccination are related but distinct outcomes. A scheduled visit may not be completed, and a completed visit does not by itself establish that MMR was administered. The record does not report participant-level links among these outcomes or mediation analyses.

Unadjusted secondary findings carry less weight because several outcomes and comparisons create more opportunities for apparently notable results to arise by chance. A multiplicity adjustment or a prespecified hierarchy can help interpret such a family of tests, but neither is reported in the registry record. The record also does not state which secondary contrasts were planned in advance. Accordingly, a nominally small p-value for a secondary comparison should be treated as exploratory unless the analysis plan establishes otherwise.

There are also limits to cross-outcome interpretation. The outcomes use different assessment windows, and the primary outcome has age-specific timing. Subgroup results by age are not reported in the registry record. The arm descriptions are blank, so the pattern cannot be tied confidently to a specific combination of automated and personal contact. The secondary results add context about scheduling and completion, but do not settle the uncertainty in the primary vaccination comparison.

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

• Appointment Scheduled
• Appointment Completed

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary analyses use logistic regression and report risk ratios. A risk ratio compares the probability of an outcome in one group with the probability in another group. A value of 1 represents equal risk; a value above 1 indicates a higher estimated risk in the first group named by the analysis, and a value below 1 indicates a lower estimated risk. The registry gives the comparisons as Arm 1 against other arms, but interpretation of which strategy those contrasts represent is limited because the arm descriptions are blank.

What does the risk difference add?

A risk difference expresses the contrast by subtracting one group’s event risk from the other group’s event risk. It is an absolute-scale measure, whereas a risk ratio is a relative-scale measure. The posted recalculations use simple unadjusted risk differences based on the event counts and arm denominators. They are descriptive contrasts and do not account for covariates or any analysis structure beyond the summary counts. The risk-difference estimates can be useful for understanding the absolute scale of the contrast, but they are not the sponsor’s reported primary model estimates.

How should the confidence intervals be read?

A confidence interval describes the range of values reasonably compatible with the data and the method used to calculate it. It reflects uncertainty in an estimate; it is not a range containing a known true value with certainty. For risk ratios, the value 1 marks no relative difference. For risk differences, the value 0 marks no absolute difference. When an interval includes that no-difference value, the data do not clearly distinguish the estimate from no difference under the method used. An interval that includes no difference does not establish equality, and an interval excluding no difference does not by itself establish practical importance or eliminate concerns about bias, measurement, or multiplicity.

What does a p-value indicate?

A p-value describes how incompatible the observed data are with a specified null hypothesis, under the statistical model and its assumptions. It is not the probability that the null hypothesis is true, nor is it a measure of the size or importance of an effect. Smaller p-values generally indicate greater incompatibility with the null model, but they do not account automatically for the number of outcomes or comparisons examined. The registry record does not report a multiplicity adjustment or a prespecified threshold for the full set of analyses.

What is the role of the sponsor’s model?

Logistic regression models the log odds of a binary outcome. The sponsor reports risk ratios from logistic regression, but the registry record does not give the full model specification, covariates, handling of clustering, or details of how model estimates were converted to risk ratios. The posted recalculations use the arm-level counts and are unadjusted. Because the record flags a discrepancy, the sponsor’s own reported analysis takes precedence over the recalculated results. The recalculations remain useful as a transparent descriptive check, but they should not be represented as a reconstruction of the sponsor’s full model.

What can the factorial label establish?

A factorial design can evaluate intervention components and, depending on the design and analysis, whether components act differently in combination. This is a general description of the design concept, not a claim about the specific contrasts used in this trial. Although the registry labels the model factorial and lists several outreach components, it does not report the factor definitions, arm-to-factor mapping, interaction estimates, or planned factorial contrasts. The reported pairwise arm comparisons therefore cannot be assumed to be estimates of factorial main effects or interactions.

What assumptions matter for binary outcomes?

Binary outcome analyses depend on how events and denominators are defined, whether observations are independent under the model, and how missing or unobserved outcomes are handled. Random allocation can support a fair comparison in expectation, but it does not resolve problems in outcome ascertainment or missing data after allocation. The registry record does not report missing-data methods, an intention-to-treat definition, exclusions from analysis, or whether all randomized participants were included in each outcome analysis. Those details are important for assessing the robustness of the estimates.

In short, the sponsor’s model-based risk ratios and the unadjusted recalculated risk differences describe the same binary endpoint on different scales and with different analysis approaches. Both require uncertainty-aware interpretation. The registry record does not contain enough methodological detail to reproduce the sponsor’s model or establish whether all planned factorial and multiplicity considerations were addressed.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an effect estimate. The primary sponsor-reported risk-ratio intervals are 0.65 to 1.09 for Arm 1 versus Arm 2, 0.85 to 1.37 for Arm 1 versus Arm 3, and 0.90 to 1.44 for Arm 1 versus Arm 4. Each spans the no-difference value of 1. The estimates therefore leave meaningful uncertainty about both the direction and the size of the relative contrast.

The recalculated risk-difference intervals also span 0: -0.112 to 0.022 for Arm 2 versus Arm 1, -0.047 to 0.092 for Arm 3 versus Arm 1, and -0.032 to 0.108 for Arm 4 versus Arm 1. These intervals likewise indicate that the observed summaries are compatible with no absolute difference. Because the registry record flags a discrepancy, the sponsor’s own analyses take precedence; the recalculated intervals are not a replacement for them.

Confidence intervals are more informative than a yes-or-no reading of a significance threshold because they show a range of estimates compatible with the data under the chosen method. Their width depends on the amount of information and the variability in the data, as well as the analysis method. The arm denominators are close in size, but the registry record does not state the original precision target or design assumptions, so it is not possible to judge the observed precision against the trial’s intended target.

Interpretation should also account for the multiple arms, outcomes, and reported comparisons. A nominal interval is not necessarily adjusted for the full set of comparisons; whether these intervals or tests were adjusted is not reported in the registry record. The uncertainty described by each interval therefore concerns its stated comparison and method, not necessarily a family of analyses considered together.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design calculation. For these binary outcomes, the figures are participants per arm, not total events. 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 trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column indicates the illustrative number of participants per arm required, under those assumptions, for an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column uses a higher target chance of detection and consequently gives a larger planning requirement for the same effect. These are design calculations, not observed power.

Rows for 100% of the observed effect use the full observed contrast as the planning target; rows for 75% and 50% use smaller target effects. Smaller effects are harder to distinguish from random variation, so they require more participants under the same assumptions. For example, for the primary Arm 1 versus Arm 2 contrast, planning for 100% of the observed effect gives 1,488 participants per arm for 80% power and 1,992 participants per arm for 90% power. Planning for 50% of the observed effect gives 6,121 participants per arm for 80% power and 8,194 participants per arm for 90% power.

These figures are sensitive to the observed effect used as their starting point. When an observed estimate is uncertain, basing a future design directly on it may give a misleading sense of the effect likely to recur. The illustrations do not establish what sample size would be appropriate for a future study; that choice would require a prespecified target effect and design assumptions, which are not reported for the original trial.

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 = 0.280; treatment proportion p₁ = 0.235; average p̄ = 0.257.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6181 = 1.2115.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6173 = 0.5196.
4. n = (1.2115 + 0.5196)² / (-0.0449)² = 1,487.8, rounded up to 1,488 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 <- 0.279635258358663                          # control proportion
p1 <- 0.234756097560976                          # 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(4567342)
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 = 1,488 (80% power), 1,992 (90% power)
 75% of observed effect: n per arm = 2,684 (80% power), 3,592 (90% power)
 50% of observed effect: n per arm = 6,121 (80% power), 8,194 (90% power)
power.prop.test: 1487.8 
Simulated power at n = 1,488 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 sponsor’s primary results are logistic-regression analyses reporting risk ratios for Arm 1 compared with Arm 2, Arm 3, and Arm 4. Those are the registry’s own model-based results. Separate recalculations use the posted event counts and denominators to estimate unadjusted risk differences, with corresponding unadjusted intervals and p-values. The estimates are related descriptions of the same binary outcome, but they differ in effect scale and analytical approach.

The registry record flags a discrepancy. For that reason, the sponsor’s own analysis takes precedence; the recalculated contrasts should be treated only as simple checks based on the posted summary statistics. They do not reproduce the logistic-regression model, and the registry record does not supply enough detail to reconstruct that model’s specification. A difference between model-based and unadjusted results should not be resolved by selecting whichever estimate appears more favorable.

The sponsor’s reported Arm 1 comparisons for the primary outcome have confidence intervals that include 1. This is consistent with the uncertainty seen in the recalculated risk-difference intervals, which include 0. The two approaches are not interchangeable, and their agreement on broad uncertainty does not remove the record’s discrepancy flag. The sponsor’s model remains the principal reported analysis, while the unadjusted calculations provide an additional descriptive view rather than a competing primary result.

The registry also lists sponsor analyses for some secondary comparisons. They should be read as reported tests within a larger set of outcomes and contrasts, not as proof of an overall pattern in the absence of a stated multiplicity plan. The analysis population, model details, and handling of missing observations are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint, two secondary endpoints, four arms, and multiple pairwise analyses. Examining several outcomes and contrasts can increase the chance that at least one result appears statistically notable even when there is no underlying effect. This is the general multiplicity problem. It does not mean that any particular reported result is false; it means that isolated p-values need to be interpreted in the context of the full analysis family.

Whether the trial used a multiplicity adjustment, a prespecified testing hierarchy, or another strategy to control interpretation across comparisons is not reported in the registry record. The record also does not provide the original statistical analysis plan or identify which contrasts were prespecified. It is therefore not possible to determine from the registry whether the reported p-values should be viewed as confirmatory tests within a defined hierarchy or as nominal results across multiple analyses.

Missing-data handling and analysis populations are also not reported in the registry record. The arm-level outcome summaries give denominators, but the record does not say whether these represent all randomized participants, whether any participants were excluded after allocation, how unavailable electronic health record documentation was classified, or how missing observations were handled in the regression analyses. The record does not describe an intention-to-treat or per-protocol population.

These omissions matter because randomization protects comparisons at assignment, while exclusions or incomplete outcome ascertainment can affect the analysis after assignment. For a documented vaccination endpoint, an absent record could reflect no vaccination or unavailable documentation; the registry description does not explain how that distinction was addressed. No subgroup-specific or sensitivity analysis addressing missing data is reported in the registry record.

As a result, the posted estimates can be interpreted as reported, but their robustness to missing outcomes and multiplicity cannot be fully assessed. This is a limit of the available registry record, not evidence that the trial did or did not perform additional analyses.

16. 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’s adverse-event figures list 0 serious adverse events and 0 deaths for each arm. It also lists 0 other adverse events for each arm. The corresponding at-risk counts are 329 for Arm 1, 328 for Arm 2, 328 for Arm 3, and 327 for Arm 4. These are the figures recorded for the safety outcomes; they should not be interpreted as proof that no events occurred outside the registry’s ascertainment or reporting process.

The record does not provide serious-event terms, and no top serious adverse-event terms are listed. The timeframe for adverse-event collection, event definitions, monitoring procedures, and rules for attributing events are not reported in the registry record. Without those details, the figures cannot establish how completely or for how long events were sought.

The study’s stated purpose concerned outreach and healthcare utilization, and the registry’s primary outcome was documented MMR receipt. Safety counts are a separate part of the record and do not provide evidence about the comparative effectiveness of outreach strategies. The zero counts should therefore be read narrowly as the reported event figures, with the limitations in ascertainment detail kept in view.

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

The results describe documented MMR receipt and appointment-related outcomes across four randomized arms. The sponsor’s primary pairwise analyses compare Arm 1 with each other arm. Their confidence intervals include the risk-ratio value of 1, so the posted primary results do not clearly distinguish those comparisons from no difference. The data do not establish equivalence, because the intervals allow a range of possible effects, and the registry record does not report an equivalence objective.

These findings do not establish that all outreach approaches have the same effect, nor do they show that any particular contact strategy changed vaccination receipt. Arm descriptions are blank, and the registry record does not map individual intervention labels to arms. It is therefore not possible to identify which precise combination of automated and personal contact corresponds to each result. The factorial label alone does not supply the missing factor definitions or interaction analyses.

The secondary outcomes offer information about scheduling and completed appointments, but they measure different steps from vaccination. A secondary statistical signal is not proof that an appointment was completed or vaccination was received as a consequence of that signal. The record does not report analyses connecting individual participants’ scheduling, completion, and vaccination outcomes.

Interpretation is also limited by unreported details: the original statistical plan, multiplicity strategy, analysis populations, missing-data methods, and full regression specification are not reported in the registry record. A discrepancy is flagged between the sponsor analysis and simple recalculations, so the sponsor’s own analysis takes precedence. The recalculations should be regarded as unadjusted descriptive checks.

In practical terms, the posted results are uncertain rather than definitive about differences in the primary endpoint. They do not demonstrate benefit or lack of benefit for a treatment, and they are not a basis for medical advice. They describe a particular outreach trial, its recorded outcomes, and the limits on what can be inferred from the available registry information.

18. Why This Trial Matters Statistically

This trial is statistically informative because it places several outreach approaches within a randomized comparison and reports outcomes at different stages of care: appointment scheduling, appointment completion, and documented vaccination. Distinguishing these stages matters. A change in an administrative or access-related outcome cannot automatically be treated as a change in the clinical service ultimately received.

The record also illustrates why effect estimates and uncertainty should be read together. The primary comparisons include point estimates that vary in direction and size, while their confidence intervals include no difference. The interval widths convey that the data do not pin down a narrow range of effects. Reporting only counts or p-values would obscure this uncertainty.

A further statistical issue is the difference between model-based sponsor analyses and unadjusted checks derived from arm summaries. They may answer related questions but need not agree exactly, particularly when the model incorporates details beyond the posted counts. Here, the registry flags a discrepancy, making it important to keep the sponsor’s analysis primary and to label recalculations as descriptive rather than as a replacement.

Finally, the factorial label and multiple outcomes make prespecification especially relevant. Without arm-to-factor mapping, planned contrasts, multiplicity handling, and analysis-population details, readers cannot determine whether the reported pairwise comparisons represent the intended factorial questions or how strongly secondary findings should be weighted. The case demonstrates that a randomized label is valuable but does not, by itself, provide all information needed to assess model choices, missingness, or the full family of statistical tests.

19. 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. Most importantly, the arm descriptions are blank even though the registry lists four outreach components or approaches. The mapping between each intervention and each arm is not reported in the registry record. This prevents a direct interpretation of arm-level comparisons as a particular automated or personal contact strategy, and it prevents readers from reconstructing the factorial structure.

The primary endpoint uses electronic health record documentation, but the record does not explain how vaccination outside the documented system was handled or how missing documentation was classified. That leaves uncertainty about outcome ascertainment. The primary timeframe also differs by age group: results are reported under the stated age-specific windows, but age-stratified estimates are not reported in the registry record.

The sponsor reports logistic-regression risk ratios, but the full model specification, covariates, and analysis population are not reported. The registry does not describe missing-data handling, participant exclusions, an intention-to-treat definition, or sensitivity analyses. It also does not report the original statistical analysis plan, sample-size justification, multiplicity strategy, or whether the multiple comparisons were prespecified.

The record flags a discrepancy between the sponsor analysis and recalculations from summary statistics. The sponsor’s own results take precedence, while simple unadjusted recalculations offer only a descriptive cross-check. Finally, safety-event ascertainment procedures and timing are not reported. These limitations do not establish that methods were inadequate; they define what cannot be assessed from the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effect of Varied Outreach Methods on Appointment Scheduling, Appointment Completion, and Receipt of MMR Vaccination — NCT04567342.
• Registry record last updated 2024-08-12; status last verified 2024-08.
• Results first posted 2024-08-12.
• 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.

23. Record Summary

The registry record describes a completed randomized, single-masked, factorial trial of varied outreach methods for children age 12-14 months or 4 years old who were due for a well-child care visit and did not have one scheduled in the next 45 days. Enrollment is listed as 1312. The primary endpoint was documented receipt of MMR vaccination, assessed by the age-specific timeframe stated in the record.

The sponsor reported logistic-regression risk ratios for Arm 1 comparisons, with primary confidence intervals that include 1. Simple unadjusted risk-difference recalculations are also available, but a discrepancy is flagged and the sponsor’s analysis takes precedence. Appointment scheduling and appointment completion were secondary outcomes. The record lists zero serious adverse events, other adverse events, and deaths in each arm.

Arm descriptions, the original statistical plan, missing-data methods, multiplicity handling, and detailed model specifications are not reported in the registry record. These gaps limit interpretation of the factorial comparisons and the robustness of the posted analyses.