Hospital to Home Outcomes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Hospital to Home Outcomes (NCT02081846), a randomized na study. The primary outcome is Number of Participants With Any Occurrence of Unplanned Re-hospitalization and/or Any Emergency/Urgent Care Visits Within 30 Days of Hospital Discharge.

2. Clinical Question

3. Trial Design

Hospital to Home Outcomes (H2O) was a randomized, parallel-group study comparing a nurse home visit with standard of care after hospital discharge. The registry lists single masking, but does not report who was masked or how masking was implemented. The study focused on hospitalized patients, and its stated intervention was a home nurse visit within 96 hours after discharge.

The registry lists enrollment as 1,500 and study status as completed. The recorded start date is 2015-02-02, and the primary completion date is 2017-06-30. The phase is listed as not applicable. The sponsor was Children's Hospital Medical Center, Cincinnati.

The primary outcome was a binary indicator of unplanned reutilization within 30 days after discharge. The registry describes the intervention and control assignments and identifies neighborhood poverty and complex versus noncomplex teams as stratification variables in the primary logistic-regression analysis. Further details about randomization procedures, allocation concealment, the identity of masked parties, and adherence to the assigned visit are not reported in the registry record.

The primary endpoint description says the analysis population included 1,500 randomized participants, with 751 in the intervention group and 749 in the control group, excluding two intervention participants who withdrew after randomization. The posted primary outcome arm counts instead show 749 participants in each group. The record does not explain this difference. Posted results for the primary endpoint and three utilization-related secondary outcomes are available; other named secondary measures do not have outcome results in the registry 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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The analysis population includes the total 1,500 (751 intervention, 749 control) randomized excluding the two subjects withdrawn in the intervention group after randomization (1 due to invalid consent, 1 requested withdrawal).

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 Any Occurrence of Unplanned Re-hospitalization and/or Any Emergency/Urgent Care Visits Within 30 Days of Hospital Discharge, measured over 30 days post-discharge.

The primary endpoint records whether a participant had any unplanned rehospitalization and/or any emergency-department or urgent-care visit within 30 days after hospital discharge. A participant who had one or more qualifying events is counted as having an occurrence; the endpoint does not quantify the number of events per participant. The registry describes the outcome as a dichotomized indicator of unplanned reutilization.

This type of endpoint captures whether a participant experienced at least one use of acute care outside the planned pathway during the specified follow-up period. In general, a binary endpoint can be interpreted in terms of the proportion of participants with an event, and it avoids treating multiple events in one participant as if they were separate participants. That simplicity also means it does not distinguish between a participant with one event and a participant with repeated events.

The registry states that the primary comparison was to use logistic regression, including neighborhood poverty and complex versus noncomplex teams as stratification variables. The endpoint is clinically focused on post-discharge care utilization, but it combines rehospitalization with emergency-department and urgent-care visits. The record does not report how event severity or the different components were weighted, nor does it provide separate primary-outcome estimates for each component.

7. Results Posted in the Registry

• Home Nurse Visit: 17.8% (133/749) versus 14.0% (105/749) on control; risk difference 3.7 percentage points (95% CI 0.0 to 7.4), risk ratio 1.27 (1.00–1.60); unadjusted two-proportion z-test p = 0.048.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Number of Participants With Occurrence(s) of an Unplanned Readmission Within 30 Days Post-discharge

• 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:
  • Home Nurse Visit: 7.7% (58/749) versus 5.5% (41/749) on control; risk difference 2.3 percentage points (95% CI -0.2 to 4.8), risk ratio 1.41 (0.96–2.08); unadjusted two-proportion z-test p = 0.077.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Home Nurse Visit and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Occurrence(s) of an Emergency Department Visit Within 30 Days Post-discharge

• 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:
  • Home Nurse Visit: 10.0% (75/749) versus 7.2% (54/749) on control; risk difference 2.8 percentage points (95% CI -0.0 to 5.6), risk ratio 1.39 (0.99–1.94); unadjusted two-proportion z-test p = 0.053.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Home Nurse Visit and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Occurrence(s) of 14-day Unplanned Healthcare Utilization

• 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:
  • Home Nurse Visit: 17.6% (132/749) versus 14.7% (110/749) on control; risk difference 2.9 percentage points (95% CI -0.8 to 6.7), risk ratio 1.20 (0.95–1.51); unadjusted two-proportion z-test p = 0.122.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Home Nurse Visit and the control. The interval gives the range of effects that remain compatible with the data.

The available secondary utilization outcomes have a broadly similar direction to the primary comparison: the posted counts are higher in the Home Nurse Visit group. However, the evidence across these outcomes is not uniform in strength, and the registry-reported p-values do not make the secondary findings a substitute for the primary analysis. They are best treated as supporting context rather than independent confirmation.

These secondary measures address related but not identical aspects of post-discharge care. Thirty-day readmission and emergency-department use are separate components of the broader primary utilization concept, while the 14-day measure uses a different follow-up window and refers to unplanned healthcare utilization. Agreement in direction can be informative, but overlap in the outcomes means the measures should not be treated as wholly independent signals.

The registry lists additional secondary outcomes, including coping difficulty, days until normalcy, and red flags remembered. Their numerical findings are not reported in the registry record. As a result, the full pattern across the planned secondary outcomes cannot be assessed from the posted results.

Unadjusted secondary results carry less weight because the registry does not report a multiplicity strategy or adjustment for examining multiple outcomes. When many outcomes are tested, the chance of at least one apparently notable result can increase. In general, multiplicity methods address that concern, but no such method is reported. The secondary p-values should therefore be read cautiously, with attention to the outcome definitions, relatedness of the measures, and the primary result, rather than interpreted as separate definitive tests.

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

• Post Discharge Coping Difficulty Scale
• Days Until Normalcy
• Red Flags Remembered
• Number of Participants With Occurrence(s) of an Unplanned Readmission Within 30 Days Post-discharge
• Number of Participants With Occurrence(s) of an Emergency Department Visit Within 30 Days Post-discharge
• Number of Participants With Occurrence(s) of 14-day Unplanned Healthcare Utilization

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant is classified according to whether any qualifying event occurred during the 30-day period. The posted counts are therefore numbers of participants with an event, rather than numbers of all events. This distinction matters because one participant with repeated utilization still contributes one event-positive participant to this endpoint.

What does the risk difference describe?

The risk difference compares the observed event proportions between the Home Nurse Visit and control groups. Its estimate is 0.037, with a confidence interval from < 0.001 to 0.074. A positive value means the observed event proportion was higher in the nurse-visit arm in this comparison. The risk difference is an unadjusted summary based on the posted arm counts; it does not incorporate the stratification variables named in the registry’s primary model.

In general, risk differences express an absolute contrast on the probability scale. They can be useful because the contrast stays in the same units as the event probability, rather than expressing a relative comparison. The interpretation remains descriptive of the posted counts, and the uncertainty interval should be considered alongside the estimate.

Why use logistic regression?

The registry says the primary group comparison was evaluated with logistic regression and included neighborhood poverty and complex versus noncomplex teams as stratification variables. Logistic regression is a general method for relating a binary outcome to group assignment and other included variables. It models the log odds of the outcome and can account for specified covariates or stratification factors. The registry does not report the model coefficient, adjusted odds ratio, confidence interval, or additional model details, so those quantities cannot be interpreted from the record.

The registry’s primary p-value is 0.047. A p-value describes how compatible the observed data are with a specified null model under the assumptions of the analysis; it is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The p-value for the recalculated unadjusted comparison is 0.048. The close values do not make the analyses identical: one is the registry’s regression result and the other is a calculation from arm-level summary counts.

How should the confidence interval be read?

In general, a confidence interval communicates a range of effect values reasonably compatible with the data and the method used to calculate the interval. It conveys precision as well as direction. The primary risk-difference interval extends from < 0.001 to 0.074, so the data are compatible with values near zero as well as larger positive differences. A confidence interval is not a guarantee that the true effect lies within its endpoints, and it does not account for uncertainties omitted from the analysis, such as unreported missing-data procedures.

Why do the adjusted and unadjusted results differ?

Adjustment can change an estimate or its uncertainty because the regression model incorporates the specified stratification variables, whereas an unadjusted calculation uses only the group counts. The registry reports the adjusted-model p-value but does not report an adjusted effect estimate or its confidence interval. Consequently, the posted unadjusted risk difference and interval should not be presented as if they were the model’s adjusted estimates. The record does not report enough model output to reconstruct or assess the adjusted result in detail.

The primary outcome’s analysis population description also deserves attention. It states that two intervention participants were excluded after randomization and gives group counts before those exclusions, while the posted primary result uses equal arm counts. The record does not explain the discrepancy, or whether other analysis-population rules were applied. Such details affect the interpretation of any analysis because the group counts and inclusion rules define which observations contribute to an estimate.

For the secondary outcomes, the registry reports logistic regression and p-values but does not provide adjusted effect estimates or confidence intervals. The unadjusted recalculations use the posted event counts. As with the primary outcome, those recalculations are useful descriptive comparisons, not replacements for the trial’s reported model-based results. The registry does not report diagnostic checks or additional assumptions for the regression analyses.

11. Confidence Intervals and Precision

The primary unadjusted risk difference is 0.037, and its 95% confidence interval runs from < 0.001 to 0.074. The interval includes values close to zero as well as larger positive differences. This means the estimate’s direction is positive in the recalculation, but its exact size is not pinned down precisely. The lower endpoint is particularly close to zero, making the distinction between a very small difference and a more substantial one uncertain.

In general, a confidence interval is a way to express sampling uncertainty around an estimate under the method’s assumptions. A narrower interval indicates greater precision than a wider interval on the same scale. The interval does not capture every source of uncertainty: it cannot resolve the primary analysis-population discrepancy, missing-data handling, outcome classification, or any limitations in the model or registry reporting.

The registry reports p = 0.047 for its adjusted logistic-regression analysis. The recalculated unadjusted p-value is 0.048. These values are not a substitute for the confidence interval, and neither value conveys the magnitude or practical importance of the group difference. The registry does not report a confidence interval for the adjusted model estimate, limiting direct assessment of its precision.

The secondary recalculated confidence intervals are also broad enough to include values close to no difference for the readmission, emergency-department, and 14-day utilization outcomes. They do not establish that the groups are equivalent; rather, they show that the available estimates leave uncertainty about the size and direction of the underlying differences. The registry does not report adjusted confidence intervals for these secondary analyses.

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 figures are illustrations based on the observed effect, not the trial’s original design assumptions. The registry does not report the trial’s own sample-size justification or design assumptions. The listed assumptions for these calculations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is a stated fraction of the observed effect.

For this binary primary endpoint, the figures are participants per arm. The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under the listed assumptions. The 90% power column gives the corresponding planning figure for a 90% chance. These are conditional planning quantities, not guarantees about a future study’s result.

The calculations show the relationship between the effect size chosen for planning and the sample size needed: planning to detect a smaller effect requires more participants. For example, the primary endpoint illustration gives 1,500 participants per arm for planning around 100% of the observed effect at 80% power, compared with 5,713 per arm when the target is 50% of the observed effect. Those figures depend on treating the observed effect as a planning reference; a future study’s true effect could differ.

These figures are not observed power. Observed power is not a useful substitute for interpreting the trial’s estimate and uncertainty after data have been collected. The confidence interval and the reported analysis results are more informative for understanding what the trial observed. The illustrations are best read as hypothetical design scenarios, not as a retrospective assessment of whether the completed study was adequately powered.

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 = 0.140; treatment proportion p₁ = 0.178; average p̄ = 0.159.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5170 = 1.0133.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5163 = 0.4345.
4. n = (1.0133 + 0.4345)² / (0.0374)² = 1,499.9, rounded up to 1,500 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 <- 0.14018691588785                          # control proportion
p1 <- 0.177570093457944                          # 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(2081846)
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 = 1,500 (80% power), 2,008 (90% power)
 75% of observed effect: n per arm = 2,604 (80% power), 3,485 (90% power)
 50% of observed effect: n per arm = 5,713 (80% power), 7,648 (90% power)
power.prop.test: 1499.9 
Simulated power at n = 1,500 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as logistic regression, with p = 0.047 for the comparison between the Home Nurse Visit and control groups. The outcome description says the model included neighborhood poverty and complex versus noncomplex teams as stratification variables. The record does not report the adjusted effect estimate or its confidence interval, so the size and precision of the adjusted contrast cannot be read from the reported p-value alone.

The unadjusted recalculation from the posted primary arm counts gives a risk difference of 0.037, with a 95% confidence interval from < 0.001 to 0.074, and p = 0.048. It uses the summary counts without the regression adjustment described for the sponsor analysis. Its role is to offer a simple descriptive comparison; it is not a replication of the sponsor’s model.

The two p-values are close, but the distinct methods mean they should not be treated as interchangeable. The record does not flag a discrepancy between the sponsor’s result and the recalculation. For inference about the prespecified primary analysis, the registry’s reported regression result is the trial’s own analysis; the recalculation adds context about the posted counts without superseding that analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a plan for handling multiplicity across the primary and secondary outcomes. It lists several secondary measures and reports analyses for utilization outcomes, but does not state whether a testing hierarchy, adjustment procedure, or other strategy was prespecified. In general, testing multiple outcomes can increase the chance of obtaining at least one statistically notable result by chance. Without a reported multiplicity plan, secondary p-values are exploratory in interpretation and should not be treated as if each were the sole confirmatory test.

Missing-data procedures are not reported in the registry record. The record does not explain how participants with unavailable outcome information were handled, whether follow-up was complete, or whether sensitivity analyses were conducted. These details matter because the endpoint depends on observing post-discharge events during a defined follow-up period. The posted counts alone do not establish that outcomes were available for every participant in the analysis population.

The primary endpoint description gives an analysis population of 1,500 randomized participants, identifying 751 in the intervention group and 749 in control before exclusion of two intervention participants after randomization. The posted primary outcome counts instead give 749 participants per arm. The record does not reconcile these figures or specify the final analysis population beyond the statement that the two withdrawals were excluded. This makes it difficult to connect the population description to the denominator used for the posted outcome counts.

The registry states that the primary model included neighborhood poverty and complex versus noncomplex teams as stratification variables, but does not report the detailed model specification, covariate coding, or adjusted effect estimate and interval. It also does not report interim-analysis procedures, protocol deviations, or the trial’s original sample-size justification. Those omissions limit independent appraisal of the analysis plan and how completely the posted results reflect it.

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 reports zero serious adverse events and zero deaths in both groups. It also reports zero other adverse events in both groups. The safety risk sets are listed as 751 for the Home Nurse Visit group and 749 for control, which differ from the equal arm counts posted for the primary efficacy outcome.

These figures should be read as the adverse-event counts recorded in the registry, not as evidence that no adverse events of any kind occurred outside the registry’s definitions or reporting period. The record does not provide a list of serious event terms, and it does not report further detail about event ascertainment, duration of safety follow-up, or the relationship of events to the intervention. Zero recorded events therefore describes the registry’s reported counts; it does not resolve broader questions about safety monitoring or completeness of reporting.

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

The primary result describes a higher observed frequency of the combined 30-day unplanned reutilization outcome in the Home Nurse Visit group than in control. The unadjusted risk difference is 0.037, and its confidence interval ranges from < 0.001 to 0.074. The registry’s adjusted logistic-regression analysis reports p = 0.047. These results characterize the comparison in this trial; they do not establish that the visit caused the difference or explain why it arose.

The endpoint combines unplanned rehospitalization with emergency-department or urgent-care visits. It does not distinguish the severity of events, count repeated events separately, or show which component contributes most to the group difference. The separately reported secondary utilization outcomes give additional context but do not eliminate uncertainty about the combined endpoint. Other secondary measures named in the registry do not have results reported in the registry record.

The results also do not answer whether any observed difference is important to patients or families, whether it reflects a change in care-seeking, or whether the findings apply to settings beyond this study. Such interpretations require information not reported in the registry record, including details of standard care, outcome ascertainment, adherence, and the population’s characteristics.

In general, a p-value near a conventional threshold is not a direct measure of clinical importance, and a confidence interval near zero does not prove equivalence. The data leave uncertainty about the size of the difference. The primary result should be interpreted alongside the analysis-population discrepancy, the absence of reported missing-data procedures, and the limited adjusted-model output. It is a description of the evidence recorded for this trial, not a directive for care or a guarantee of outcomes in other populations.

18. Why This Trial Matters Statistically

This trial illustrates why the choice of endpoint matters in clinical research. The primary outcome combines several forms of unplanned post-discharge care into a participant-level indicator. That measure is straightforward to describe, but it does not show how many events occurred per participant or whether the group contrast was driven by readmissions, emergency visits, or urgent-care visits. Separate component outcomes can add context, while still leaving the combined endpoint as the primary question.

It also illustrates the distinction between an adjusted trial analysis and a simple comparison of group counts. The registry’s logistic regression includes named stratification variables, while the recalculation uses only the posted summary counts. The resulting p-values are similar, but the analyses address the data differently. Reporting both an adjusted effect estimate and its confidence interval would make the primary result easier to assess for magnitude and precision.

Precision matters as much as the direction of an estimate. The primary interval reaches close to zero and extends to larger positive differences, indicating uncertainty about the exact size of the group contrast. A p-value alone cannot convey that range. The interval and the outcome counts offer complementary information.

Finally, the record highlights the value of transparent reporting about analysis populations, missing data, and multiplicity. The stated primary analysis population and posted arm denominators are not reconciled, and the record does not describe missing-data handling or a secondary-outcome testing strategy. These details shape how confidently readers can connect the reported estimates to the randomized comparison and interpret secondary findings.

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 specific to the registry record constrain interpretation. The primary endpoint description gives an analysis population of 1,500 randomized participants, with 751 assigned to the intervention and 749 to control before two intervention withdrawals are excluded. The posted primary efficacy counts use 749 participants per arm. The record does not explain how these numbers relate to one another, so the endpoint denominator and final analysis population are not fully transparent.

The registry reports a primary logistic-regression p-value but does not provide the adjusted effect estimate or confidence interval. The unadjusted recalculation can describe the posted counts, but it cannot supply the missing model-based effect estimate. Details about allocation concealment, masking implementation, adherence, and outcome ascertainment are also not reported in the registry record.

The handling of missing outcomes is not reported. The record does not describe follow-up completeness, imputation, exclusions beyond the two stated withdrawals, or sensitivity analyses. It also does not report a multiplicity plan for secondary outcomes. These omissions limit evaluation of possible bias and the evidential weight of secondary findings.

The intervention is described as a nurse home visit within 96 hours of discharge, but the registry does not detail the visit’s content or the services included in standard care. Some listed secondary outcomes have no numerical results in the record, leaving the broader set of intended outcomes incompletely characterized. These limitations concern what can be established from the registry record and do not by themselves establish that the trial procedures were inadequate.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Hospital to Home Outcomes — NCT02081846.
• Registry record last updated 2019-04-16; status last verified 2019-04.
• Results first posted 2019-03-29.
• 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

Hospital to Home Outcomes was a completed randomized, parallel-group study comparing a nurse home visit within 96 hours after discharge with standard of care. The registry lists enrollment of 1,500 and identifies the primary outcome as any unplanned rehospitalization and/or emergency-department or urgent-care visit within 30 days after discharge.

The registry reports a primary logistic-regression p-value of 0.047. An unadjusted recalculation from posted counts estimates a risk difference of 0.037, with a 95% confidence interval from < 0.001 to 0.074 and p = 0.048. Posted secondary utilization outcomes generally have higher event counts in the nurse-visit arm, but no multiplicity plan is reported. The record does not reconcile the primary analysis-population description with its posted arm counts, and missing-data procedures are not reported.