Discharge Follow-up Phone Call Program: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Discharge Follow-up Phone Call Program (NCT03050918), a randomized na study. The primary outcome is Number of Participants With In-patient Re-admissions.

2. Clinical Question

This is a question about the effect of assigning a discharge-support program in a pragmatic care setting, not simply about whether a call was completed or whether a particular patient benefited. The primary outcome is a count of participants who experienced at least one inpatient readmission in the specified period. It does not count the total number of readmission episodes, and the registry does not provide a separate analysis of repeated admissions.

The comparison is between randomized groups, so the principal question concerns outcomes by assigned group. That framing matters because not every person assigned to a phone-call program will necessarily be reached or complete a call. The registry describes call attempts, but does not report how many participants were reached or how intervention receipt was handled in the primary analysis.

3. Trial Design

The registry describes a randomized, controlled, parallel-group trial of the discharge follow-up phone-call program. The enrollment is 3054. Participants were assigned to the Phone Call Group or the Usual Care Group; the posted primary outcome counts show 1534 participants in the intervention group and 1520 in usual care. The registry identifies no masking. The study is marked completed, and its listed start and primary-completion dates are 2017-02-20 and 2017-09-28.

The intervention was behavioral. The phone-call description specifies that the first attempt was to occur within 72 hours after hospital discharge, with a maximum of 3 attempts by post-discharge day 7. A study nurse made the attempts, using a semi-structured script embedded in a program-specific electronic health record. The available script description is incomplete, so further details of call content or training are not reported in the registry record. The usual-care group received standard discharge planning and follow-up according to their medical providers.

The trial is described as pragmatic and focused on a general medicine inpatient population. That setting is relevant to interpretation: the question is whether offering a follow-up call program changes outcomes amid routine discharge care, rather than whether calls can work under a tightly controlled efficacy protocol. The precise eligibility rules, sites or units involved, and methods for maintaining allocation concealment are not reported in the registry record.

The registry lists a primary outcome of participants with inpatient readmission within 30 days. It also lists secondary outcomes addressing patient satisfaction, emergency department visits, discharge-plan implementation assistance, and mortality. The record does not describe the sample-size justification, the trial’s original power assumptions, or the detailed statistical analysis plan. Those missing details limit assessment of whether the chosen enrollment was planned around a particular effect or analysis.

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 Number of Participants With In-patient Re-admissions, measured over 30 days.

The primary endpoint counts participants with an inpatient readmission during the 30 days after discharge. It is a binary outcome at the participant level: a person either had a readmission during the stated period or did not. The reported values are counts of participants, rather than a count of all admission episodes. The registry does not report whether multiple admissions for one participant were separately analyzed.

Readmission is used as an outcome because the trial’s stated purpose was to assess whether follow-up calls affect hospital readmission and other aspects of the transition from inpatient to outpatient care. In general, a post-discharge call could identify questions or barriers that arise after a patient returns home; the study description specifically mentions interest in discharge-plan implementation assistance. This is general context for why the endpoint may matter, not evidence that the program changed readmission or that any particular pathway caused an outcome.

The registry gives the timeframe as 30 days and reports 228 participants with readmissions in the phone-call group and 232 in usual care. Those counts must be interpreted relative to their respective group sizes, which differ. An unadjusted comparison of the posted summaries estimates the difference in the proportion of participants with a readmission. It does not, by itself, establish why any difference occurred, describe the timing of readmissions within the period, or capture other dimensions of recovery and care.

7. Results Posted in the Registry

• Phone Call Group (Intervention Arm): 14.9% (228/1534) versus 15.3% (232/1520) on control; risk difference -0.4 percentage points (95% CI -2.9 to 2.1), risk ratio 0.97 (0.82–1.15); unadjusted two-proportion z-test p = 0.757.

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.

Patient Satisfaction: Experience

• 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:
  • Phone Call Group (Intervention Arm): mean 8.20 versus 8.30 on control; difference -0.10 (95% CI -0.39 to 0.19), standardized effect d = -0.06; z-test p = 0.502.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Phone Call Group (Intervention Arm) and the control. The interval gives the range of effects that remain compatible with the data.

Patient Satisfaction: Likelihood to Recommend the Facility (Top Box Rating)

• 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:
  • Phone Call Group (Intervention Arm): 74.0% (168/227) versus 78.1% (193/247) on control; risk difference -4.1 percentage points (95% CI -11.8 to 3.6), risk ratio 0.95 (0.86–1.05); unadjusted two-proportion z-test p = 0.292.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Phone Call Group (Intervention Arm) and the control. The interval gives the range of effects that remain compatible with the data.

Patient Satisfaction: Hospital Experience (Top Box Rating)

• 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:
  • Phone Call Group (Intervention Arm): 68.3% (155/227) versus 69.5% (173/249) on control; risk difference -1.2 percentage points (95% CI -9.5 to 7.1), risk ratio 0.98 (0.87–1.11); unadjusted two-proportion z-test p = 0.778.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Phone Call Group (Intervention Arm) and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning patient satisfaction, emergency department visits, discharge-plan implementation assistance, and mortality. The detailed posted results represented in this analysis include patient experience and two top-box satisfaction measures. Across those satisfaction outcomes, the unadjusted comparisons do not show a consistent, clearly separated pattern favoring the phone-call group. Their estimates are close to no difference, and their confidence intervals include the no-difference value. The registry does not provide detailed results for every listed secondary outcome in the information.

These secondary findings provide context around the primary readmission comparison but do not replace it. Satisfaction captures a different aspect of the discharge experience than inpatient readmission, and a pattern in one outcome would not establish a corresponding effect on another. The trial’s stated goals also included exploratory subgroup information and discharge-plan support needs, but specific subgroup findings or complete results for those aims are not reported in the registry record.

Unadjusted secondary results generally carry less weight than a prespecified primary result because many outcomes can create multiple opportunities for apparently notable findings by chance. The registry does not report whether the secondary analyses were adjusted for multiplicity, how they were ordered, or which were considered confirmatory versus exploratory. These uncertainties make isolated secondary comparisons especially difficult to interpret as firm evidence.

The satisfaction outcomes are also based on fewer participants than the primary readmission outcome, as reflected in their posted denominators. The registry does not explain why outcome denominators vary or whether response and missingness differed between groups. As a general matter, satisfaction results may be influenced by who responds, and those responses may not represent all assigned participants. The record does not provide enough information to assess that possibility. The overall secondary pattern should therefore be read as descriptive and exploratory rather than as a separate definitive demonstration of program effects.

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

• Patient Satisfaction: Experience
• Patient Satisfaction: Likelihood to Recommend the Facility (Top Box Rating)
• Patient Satisfaction: Hospital Experience (Top Box Rating)
• Patient Satisfaction: Likelihood to Recommend the Facility
• VUMC Emergency Department (ED) Visits
• Number of Patient Received Discharge Plan Implementation Assistance
• Mortality

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: the registry reports whether each participant had an inpatient readmission within 30 days. A natural summary for a binary outcome is the proportion with the event in each group. The unadjusted recalculation compares those proportions and expresses the contrast as a risk difference, with a relative risk also reported. These are summaries of the posted group counts, not necessarily the sponsor’s prespecified analysis.

What does the risk difference express?

The risk difference subtracts the event proportion in usual care from the event proportion in the phone-call group. A value below zero means the observed proportion is lower in the intervention group; a value above zero means it is higher. The recalculated estimate is -0.004. This is a small absolute contrast in the posted data, but the estimate alone is not enough to judge how reliably the underlying effect has been estimated. Its confidence interval, from -0.029 to 0.021, is relevant because it includes zero and covers values on either side.

How does the relative risk differ?

The relative risk compares the event proportion in the phone-call group with the proportion in usual care as a ratio. A value corresponding to equal event proportions represents no relative difference. The recalculated relative risk is 0.974, and its interval from 0.823 to 1.152 includes the no-difference value. A relative measure can help describe proportional contrast, while the risk difference conveys absolute contrast. Neither measure should be read without considering the uncertainty and the event frequencies in the groups.

What does a p-value say?

The recalculated p-value is 0.757. In general, a p-value describes how compatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. A large p-value does not prove that the groups are equivalent. Equivalence would require an appropriate design and a prespecified margin for what differences would be considered acceptably small; such a margin is not reported in the registry record.

The registry lists a sponsor-reported Wilcoxon (Mann-Whitney) superiority analysis, but does not identify an analysis parameter or provide an effect estimate or interval alongside the reported p entry. Wilcoxon (Mann-Whitney) is generally a rank-based method for comparing distributions of observations between groups. Its use for a binary participant-level endpoint is not explained in the registry record, and the record does not provide enough information to reconstruct the sponsor’s analysis. The difference between that entry and the unadjusted recalculation is flagged as a discrepancy, so the sponsor’s own analysis takes precedence.

Why do randomization and analysis details both matter?

Random assignment is intended to make groups comparable, on average, at the point of assignment. It does not guarantee that every aspect of trial conduct or analysis is free from bias. Interpretation also depends on how participants were analyzed, whether outcomes were available for all assigned participants, and whether any adjustments or exclusions were used. These details are not reported in the registry record. The group counts allow a basic unadjusted comparison, but they do not resolve those reporting gaps.

In general, adjustment can account for prespecified baseline variables or improve precision, depending on the analysis plan and data. It should not be assumed that the sponsor adjusted for any variables because adjustment details are not reported in the registry record. Likewise, the available summaries do not show whether clustering, repeated outcomes, or other design features were considered. The result is therefore specifically an unadjusted recalculation from the posted summary counts.

Why can over-dispersion matter?

Over-dispersion is a general concern when outcomes vary more than a statistical model expects. It can make standard errors too small if the model assumes less variability than is present, which can make confidence intervals too narrow and tests appear more decisive. The primary outcome is a binary participant-level event, and the registry does not report a model-based analysis that would let readers assess over-dispersion. The concept is relevant generally to count and clustered data, but it should not be presented as a demonstrated problem in this trial.

The registry’s reported primary measure is a count of participants with an event. The recalculation uses the arm-level counts and denominators, without covariate adjustment. Any calculation from summaries depends on the accuracy and completeness of those summaries and cannot recover participant-level detail. It also cannot recreate a different sponsor analysis when the analysis specification and output are not reported.

11. Confidence Intervals and Precision

The 95% confidence interval for the recalculated risk difference is -0.029 to 0.021. A confidence interval describes the range of effect values compatible with the observed data under the calculation’s assumptions. It is not a guarantee that the true effect lies inside this particular interval, and it does not assign a probability to each possible value after the data have been observed.

For a risk difference, zero corresponds to equal event proportions. Because the interval includes zero, the posted counts are compatible with no difference as well as with a lower or higher proportion in the phone-call group. Its width also matters: the estimate is not precise enough to isolate a narrow range around the observed contrast. The interval does not support a claim of equivalence, because the registry does not report an equivalence margin or an equivalence analysis.

The relative-risk interval, 0.823 to 1.152, conveys uncertainty on a ratio scale. It includes the value for no relative difference. The risk-difference and relative-risk intervals are complementary descriptions of uncertainty, not independent replications. A confidence interval’s interpretation depends on the method used to calculate it; the registry record does not provide the sponsor’s interval for the primary result.

Precision is also affected by how many outcome observations are available and by the frequency of the event. The arm-level counts provide a basis for an unadjusted interval, but the record does not describe missing outcomes or the sponsor’s analysis population. Consequently, the recalculated interval should be read as conditional on the posted summaries and not as a full account of all uncertainty in trial conduct or 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 planning estimates are expressed as participants per arm, not as total events. The assumptions listed for these calculations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is a stated fraction of the observed effect. For time-to-event calculations, the stated convention is total events; the estimates relevant to these outcomes are participant counts per arm. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative participants per arm that would be needed for an analysis to have an 80% chance of detecting the specified effect under the listed assumptions, if that effect and assumptions held. The 90% power column gives the corresponding illustration for a higher chance of detecting that effect. These are planning quantities, not guarantees: actual power and precision depend on the true effect, event frequency, analysis, follow-up, and data completeness.

The rows labeled for 100%, 75%, and 50% of the observed effect show planning for progressively smaller effects relative to the observed estimate. Smaller effects are harder to distinguish from random variation, so the required participant count rises as the target effect gets smaller. The very large estimates associated with the small observed contrast should not be interpreted as evidence that a future trial must enroll those exact numbers; they illustrate the implications of the chosen assumptions and target effect.

These figures are planning illustrations, not observed power. Observed power calculated from the result after a trial is complete does not clarify the uncertainty better than the confidence interval and is not what these estimates represent. They are hypothetical designs based on the recalculated observed effect, rather than the original trial’s documented design plan.

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 = 0.153; treatment proportion p₁ = 0.149; average p̄ = 0.151.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5058 = 0.9914.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5058 = 0.4257.
4. n = (0.9914 + 0.4257)² / (-0.0040)² = 125,489.1, rounded up to 125,490 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 <- 0.152631578947368                          # control proportion
p1 <- 0.148631029986962                          # 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(3050918)
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 = 125,490 (80% power), 167,994 (90% power)
 75% of observed effect: n per arm = 223,702 (80% power), 299,473 (90% power)
 50% of observed effect: n per arm = 504,698 (80% power), 675,647 (90% power)
power.prop.test: 125489.1 
Simulated power at n = 125,490 per arm: 0.796 (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 reports a sponsor analysis for the primary outcome using Wilcoxon (Mann-Whitney) and labels the analysis as a superiority comparison. Its p entry is recorded as “.05,” but an estimate, confidence interval, test statistic, and analysis parameter are not included in that entry. The information is therefore insufficient to determine precisely how the sponsor quantified the result or how to interpret the reported p notation.

The recalculated comparison uses the posted counts and denominators without adjustment. It gives a risk difference of -0.004, a 95% confidence interval from -0.029 to 0.021, and p = 0.757. That calculation is not a reconstruction of the sponsor’s analysis: the reported method differs, and the registry flags a discrepancy. The two results should not be blended or treated as interchangeable.

Because the discrepancy flag is true, the sponsor’s own analysis takes precedence. The unadjusted recalculation is useful for describing what follows from the posted summary counts, but it should not override the sponsor’s analysis. Since the sponsor’s underlying estimate and full statistical details are not reported in the registry record, the sponsor finding cannot be independently checked from the information available in the record. This limitation is a reporting issue, not evidence that either analysis is necessarily incorrect.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and multiple secondary outcomes, including several measures of patient satisfaction. When multiple outcomes are tested, the chance of obtaining at least one apparently notable result by chance can increase. Statistical approaches to multiplicity can address this issue, for example by adjusting significance thresholds or controlling an overall error rate. The registry record does not report whether a multiplicity procedure was planned or used, whether secondary outcomes had a hierarchy, or which comparisons were intended to be confirmatory.

The record includes more than one sponsor-reported analysis entry for some satisfaction outcomes, with different listed methods. It does not explain whether these represent alternative tests, separate analysis populations, or another reporting structure. No additional interpretation should be inferred from the presence of multiple entries. The detailed statistical analysis plan, including the relationship between primary and secondary tests, is not reported in the registry record.

Missing data are another concern for outcomes that depend on follow-up or survey response. The satisfaction outcomes are reported for smaller groups than the primary endpoint, but the registry does not state why those denominators differ, whether observations were missing, how missingness was defined, or whether any imputation or sensitivity analysis was conducted. It is not possible to conclude from the denominators alone that missingness biased the results, or that it had no effect.

The analysis population is also not specified in enough detail. The record does not say whether the sponsor analyzed all randomized participants as assigned, excluded participants after randomization, or used another population definition. For the phone-call group, the record describes attempted calls but does not report reach or completion counts. Consequently, the primary group comparison cannot be connected to intervention receipt from the registry summaries alone.

Interim analyses, stopping rules, and outcome adjudication procedures are not reported in the registry record. Their absence from the record should be treated as a reporting gap, not proof that they were absent from trial conduct. These limitations affect assessment of the analysis strategy and certainty, while leaving the posted counts and the basic unadjusted recalculation interpretable as summaries of the information recorded.

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 data list zero serious adverse events and zero other adverse events in each group. These entries describe what was recorded in the registry under those categories; they do not establish that no health problems occurred. The registry does not provide serious-event terms, and it does not explain the definitions, reporting window, collection procedures, or completeness of adverse-event ascertainment.

The adverse-event record also lists 68 deaths in the phone-call group and 75 in usual care. These are counts, and the record does not provide timing, causes, participant-level follow-up, or a statistical comparison for these figures. They should not be treated as an estimate of a treatment effect or as evidence about the cause of death. Mortality is also listed among the secondary outcomes, but a detailed mortality analysis is not reported in the registry record.

Safety interpretation requires the outcome definitions and follow-up context, not counts alone. The available data do not establish whether events were actively sought, whether reporting was complete, or how the listed death counts relate to the mortality endpoint analysis. Accordingly, the entries should be read as limited registry reporting rather than a comprehensive safety assessment.

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

The result means that the posted primary outcome counts were similar in the two randomized groups, and the unadjusted recalculation is compatible with a range of effects that includes no difference. The estimate points toward a slightly lower event proportion in the phone-call group, but its uncertainty does not support a confident conclusion that the program reduced readmission. The interval also does not establish that the groups are equivalent or that any possible difference is unimportant.

The result does not say whether a particular patient would have been reached by a call, whether the call addressed a specific need, or whether the program changed the quality of transition support. It does not measure all aspects of recovery or the number of readmission episodes. The registry’s broader objectives include satisfaction, emergency department use, mortality, and implementation assistance, but the available primary comparison answers only the 30-day inpatient readmission question.

The unadjusted recalculation should not be mistaken for the sponsor’s full analysis. The registry marks a discrepancy, and the sponsor’s own analysis takes precedence. At the same time, the sponsor’s reported method and p entry are not accompanied by enough detail to reproduce or fully interpret that analysis. The appropriate conclusion is therefore constrained both by the uncertainty in the posted counts and by incomplete reporting of the sponsor analysis.

More generally, a trial result is evidence about a comparison under the study conditions, not a guarantee that the same outcome will occur in another setting. The registry describes a pragmatic program in a general medicine inpatient population, but detailed eligibility, setting, delivery, and analysis information is limited. The findings should not be extended to populations or call programs that the record does not describe.

No medical decision follows from these registry statistics alone. They describe a trial comparison and its precision; they do not provide individual-level predictions, establish a mechanism, or demonstrate that the intervention is beneficial or harmful.

18. Why This Trial Matters Statistically

This trial raises a useful statistical question about how to evaluate a relatively simple transition-support intervention in routine care. Random assignment creates a framework for comparing outcomes by assigned group, while the pragmatic setting makes implementation and actual reach relevant to interpretation. The registry describes attempted calls but does not report how many participants were reached, so the distinction between assignment to a program and receipt of its intended elements remains important.

The primary endpoint illustrates why estimates and uncertainty should be read together. Group counts alone can appear close, but a statistical comparison also needs denominators and an interval to show how much uncertainty remains. Here, the recalculated interval spans values on both sides of no difference. This calls for a cautious reading rather than treating either the point estimate or the p-value as a complete answer.

The record also demonstrates the importance of transparent analysis reporting. A sponsor-reported method and p entry are present, but there is no accompanying estimate or interval, and the record flags a discrepancy with a simple recalculation. Without a detailed analysis plan and fuller results, readers cannot determine how the sponsor’s method relates to the summary counts. Reproducible reporting would help distinguish a difference in method from a data or reporting issue.

Finally, multiple secondary outcomes can broaden understanding of a complex intervention, but they require clear prespecification and careful interpretation. Satisfaction, readmission, emergency department use, mortality, and discharge assistance reflect different facets of care. Their results should not be combined into a single claim, particularly when multiplicity handling and missing-data methods are not reported. The trial is statistically instructive both for its randomized comparison and for the limits imposed by incomplete registry detail.

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.

The registry record leaves important design and analysis details unresolved. Eligibility criteria and the precise clinical setting are not reported in the registry record, limiting assessment of which patients the findings most directly represent. Although the study is described as pragmatic, details about implementation across routine services, the extent of usual-care variation, and fidelity to the call program are not available.

The intervention description states the intended call-attempt window but does not report how many participants were reached, how many attempts were made in practice, or what assistance participants received. The script description is incomplete. Without those details, the comparison cannot show whether outcomes relate to actual exposure to calls or to the offer of the program as assigned.

For the primary analysis, the registry does not report a detailed analysis population, missing-outcome procedures, covariate adjustment, or a full sponsor estimate and confidence interval. The discrepancy between sponsor reporting and the unadjusted recalculation limits independent verification. The record also does not report the trial’s original sample-size justification or prespecified design assumptions.

Secondary-outcome reporting is incomplete in the information available, and the registry does not describe multiplicity handling. Satisfaction outcomes have smaller reported denominators, without an explanation of response or missingness. The adverse-event entries lack definitions and collection details, while death counts are not accompanied by timing or an analysis. These limitations do not invalidate the listed summaries, but they restrict the conclusions that can be drawn from them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Discharge Follow-up Phone Call Program — NCT03050918.
• Registry record last updated 2019-07-29; status last verified 2019-07.
• Results first posted 2019-07-29.
• 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 describes a completed, randomized, parallel-group, unmasked pragmatic trial of a hospital discharge follow-up phone-call program, sponsored by Vanderbilt University Medical Center. Enrollment was 3054. The intervention involved attempted follow-up calls after discharge, compared with standard discharge planning and usual provider follow-up.

The primary endpoint was participants with inpatient readmission within 30 days. The posted counts were 228 in the phone-call group and 232 in usual care. An unadjusted recalculation gives a risk difference of -0.004, with a 95% confidence interval from -0.029 to 0.021 and p = 0.757. The interval includes no difference, and the registry flags a discrepancy with the sponsor-reported analysis. The sponsor’s own analysis takes precedence, although its full result is not reported in the registry record.

The registry lists secondary outcomes in satisfaction, emergency department use, discharge-plan assistance, and mortality. Important details about missing data, multiplicity, analysis populations, and the original sample-size plan are not reported in the registry record. The posted summaries therefore support a cautious description of the trial comparison, not a definitive claim about the program’s effect.