Intervention to Improve Expression of End of Life Preferences for Homeless Persons: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Intervention to Improve Expression of End of Life Preferences for Homeless Persons (NCT00546884), a randomized na study. The primary outcome is Completion of Advance Directive.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group behavioral study with no masking. It lists an enrollment of 262 and marks the study as completed. The listed study dates are 2007-11 for the start and 2008-08 for primary completion. Phase is recorded as not applicable. The University of Minnesota is listed as sponsor.

The two conditions were Minimal Intervention and Guided Intervention. In the minimal condition, participants received an advance directive and written instructions. In the guided condition, participants were invited to meet individually with a health care professional specializing in end-of-life care. The registry does not describe additional contact, adherence procedures, or how the interventions were delivered in practice.

The primary outcome was a binary participant count: completion of an advance directive. The outcome timeframe is recorded as 21 months. The posted group results list 15 participants with the outcome among 117 in Minimal Intervention and 55 among 145 in Guided Intervention. The registry’s enrollment entry and these group counts are reported as recorded; no reconciliation or participant-flow account is available.

Randomization can support a fair comparison when allocation is implemented as planned and outcome data are sufficiently complete, but important details for assessing those conditions are not reported in the registry record. The method used to generate or conceal the allocation sequence, any stratification, and the analysis population are not reported. No masking was used, and the record does not say whether outcome assessment was independent of intervention delivery.

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 Completion of Advance Directive, measured over 21 months.

The primary endpoint is Completion of Advance Directive. It counts participants who completed an advance directive for their health care in the circumstance that they could not direct their own care. The registry classifies the endpoint as a binary count of participants with an event and gives a timeframe of 21 months.

This outcome directly addresses the stated question about whether homeless persons complete an advance directive and whether guidance is associated with completion. A completion count is readily interpretable as an event occurrence, rather than a rating or time-to-event measure. It also focuses on a concrete action that the intervention was intended to address.

As a general statistical point, an endpoint should be defined clearly enough that the same event is counted consistently across study groups. The registry’s short description identifies the event, but does not report detailed criteria for what qualified as a completed directive, how completion was verified, or how the timeframe was applied to participants with incomplete follow-up. Those definitions and procedures are not reported in the registry record.

The brief summary also mentions interest in whether completing a living will affects care at the end of life. The sole posted outcome measure is directive completion; the record does not report a separate outcome measuring subsequent end-of-life care. Thus the primary endpoint informs the completion question, not the stated broader question about care received.

7. Results Posted in the Registry

• Guided Intervention: 37.9% (55/145) versus 12.8% (15/117) on control; risk difference 25.1 percentage points (95% CI 15.2 to 35.1), risk ratio 2.96 (1.77–4.96); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: each participant either had a completed advance directive recorded or did not. The registry reports counts by randomized group and an unadjusted comparison. The outcome is not reported as a continuous measurement or as time until completion. The reported timeframe is 21 months, but the operational details for determining whether a participant completed the directive within that period are not reported in the registry record.

What does a risk difference describe?

A risk difference compares the proportion with the outcome in one group with the proportion in the comparison group. The recalculated estimate is 0.251, with a confidence interval from 0.152 to 0.351. It is an absolute-scale measure: it expresses the estimated difference between the observed group proportions, rather than how many times one proportion is the other. The registry lists the guided group as the intervention group and Minimal Intervention as the control.

The risk difference is often useful because absolute differences can be easier to relate to a decision context than relative measures. However, interpretation still depends on the study population, outcome definition, follow-up, and completeness of data. The estimate is unadjusted; it does not account for covariates. Whether an adjusted analysis was performed by the sponsor is not reported in the registry record.

How do risk ratios and odds ratios differ?

A risk ratio compares the outcome proportions across groups. The recalculated risk ratio is 2.959, with a confidence interval from 1.765 to 4.958. An odds ratio compares odds, where odds are the number with an event relative to the number without it. The recalculated odds ratio is 4.156, with a confidence interval from 2.197 to 7.861. Since odds and proportions are different quantities, an odds ratio should not be read as though it were a risk ratio. The apparent magnitude of a contrast can differ across these scales.

The sponsor’s reported method is described as Chi-squared and its reported parameter as Odds Ratio. The sponsor reports an odds ratio of 4.16 and p < 0.05. The registry does not give a confidence interval for that result. The recalculated odds ratio is close in displayed value, but the record marks a discrepancy, and the sponsor’s own analysis takes precedence. The record does not explain which data, method choices, or reporting details account for the marked discrepancy.

What does a chi-squared test assess?

As a general statistical explanation, a chi-squared test can assess whether categorical outcome distributions differ between groups, under assumptions related to the data and test. It does not by itself describe the size of a difference; an effect estimate such as an odds ratio or risk difference provides that complementary information. A p-value measures how unusual results at least as incompatible with a specified null model would be if that model and test assumptions held. It is not the probability that the null hypothesis is true, and it does not quantify the chance that the result is due to bias.

The sponsor’s p-value is reported as p < 0.05, while the recalculated unadjusted comparison has p < 0.001. Because the registry marks a discrepancy, these should not be collapsed into one value or treated as independent confirmation. The sponsor’s result is the study’s reported analysis; the recalculated result describes a separate unadjusted calculation from the posted summary statistics.

Why can over-dispersion matter?

As a general concept, over-dispersion occurs when observed variation exceeds what a statistical model expects. It is particularly relevant for outcomes modeled as counts or rates, where ignoring extra variation can make uncertainty appear too small. This primary outcome is recorded as a binary participant count, and the registry does not report a count-rate model or an over-dispersion assessment. There is therefore no basis in the record to say that over-dispersion was assessed or affected the analysis. The general concept should not be mistaken for a reported feature of this study.

What analysis details are unavailable?

The registry does not report the allocation-sequence method, concealment procedures, a detailed statistical analysis plan, covariate adjustment, interim analyses, missing-data methods, or a defined analysis population. It also does not report whether the primary analysis followed assignment regardless of intervention received. Such details matter because analysis choices can affect both the estimate and its uncertainty. Their absence from the registry record does not show that the procedures were absent from the study; it means they cannot be evaluated from the record.

The reported uncertainty intervals accompany the recalculated unadjusted comparisons. The registry does not explain their calculation method. General statistical interpretation treats an interval as a range of values compatible with the data and method at the stated confidence level, not as a range that captures all sources of uncertainty. In particular, an interval based on summary counts does not account for unreported biases, outcome-definition issues, or missing-data assumptions.

10. Confidence Intervals and Precision

The recalculated risk difference is 0.251, with a confidence interval from 0.152 to 0.351. This interval conveys sampling uncertainty under the calculation used. It indicates that the posted counts are compatible with a range of risk differences, rather than identifying an exact underlying contrast. The interval does not incorporate every uncertainty that could arise from study conduct, outcome measurement, or incomplete reporting.

The recalculated risk ratio is 2.959, with a confidence interval from 1.765 to 4.958. The recalculated odds ratio is 4.156, with a confidence interval from 2.197 to 7.861. Each interval is on its measure’s own scale, so the values should not be compared as if they were the same type of effect. The registry does not provide a confidence interval for the sponsor’s reported odds ratio of 4.16.

As a general explanation, a confidence interval reflects how much an estimate would vary across repeated studies under the assumptions of the method. It does not mean there is a stated probability that this particular interval contains the true effect, and it does not address systematic error. The observed group counts and the width of an interval are relevant to precision, but precision is not the same as validity or practical importance.

The marked discrepancy between the sponsor analysis and recalculation is also relevant to reading precision. The recalculated intervals describe the unadjusted summary-statistic comparisons, not necessarily the sponsor’s analysis. The reason for the discrepancy and the sponsor analysis’s interval are not reported in the registry record. These limits should be kept in view when interpreting how precisely the study estimated the contrast.

11. 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 assumptions. They give participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. The trial’s own sample-size justification and original planning assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for 80% power under those assumptions. In general, power is the probability that a study will meet its statistical criterion if the effect used for planning is the true effect and the assumptions hold. The 90% power column gives the corresponding planning figure for 90% power. Greater planned power generally requires a larger sample when other assumptions remain the same.

The rows describe planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For planning for 100% of the observed effect, the figures are 46 participants per arm for 80% power and 62 participants per arm for 90% power. For planning for 75% of the observed effect, they are 76 and 101 participants per arm, respectively. For planning for 50% of the observed effect, they are 153 and 204 participants per arm, respectively. Smaller effects need more participants to detect under the same assumptions.

These are not observed power figures. They are illustrations of how planning requirements change when the assumed effect size or desired power changes. They should not be read as evidence about the probability that this completed study detected its effect, nor as a statement of the study’s actual design rationale.

12. 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 = 0.128; treatment proportion p₁ = 0.379; average p̄ = 0.254.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6154 = 1.2062.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5892 = 0.4959.
4. n = (1.2062 + 0.4959)² / (0.2511)² = 45.9, rounded up to 46 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 <- 0.128205128205128                          # control proportion
p1 <- 0.379310344827586                          # 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(546884)
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 = 46 (80% power), 62 (90% power)
 75% of observed effect: n per arm = 76 (80% power), 101 (90% power)
 50% of observed effect: n per arm = 153 (80% power), 204 (90% power)
power.prop.test: 45.9 
Simulated power at n = 46 per arm: 0.807 (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.

13. Analyses Reported by the Sponsor

The registry reports a sponsor analysis using a Chi-squared method, with an odds ratio of 4.16 and p < 0.05. It does not report a confidence interval for that analysis. A separate unadjusted recalculation from the posted summary statistics gives an odds ratio of 4.156, with a confidence interval from 2.197 to 7.861, and p < 0.001. The recalculated comparison also reports a risk difference and risk ratio.

The registry explicitly marks a discrepancy between the sponsor analysis and the recalculation. The sponsor’s own analysis takes precedence as the study’s reported result; the recalculation is not a correction or replacement for it. The small difference between the displayed odds-ratio values does not resolve the discrepancy, since the reported p-values differ and the record does not explain the underlying analysis choices or data.

The record does not describe whether the sponsor used a different analysis population, method, data version, or other procedure. Those possibilities should not be assumed. The sponsor’s analysis and the unadjusted recalculations are best read as distinct results with different reporting detail, and the discrepancy remains unexplained in the registry record.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists one outcome measure and one analysis. No secondary outcomes are posted. The brief summary describes a broader interest in whether completing a living will affects care at the end of life, but the registry’s listed outcome is completion of an advance directive. It does not provide a posted analysis of subsequent care. The relationship between the broader study aim and the outcomes actually reported therefore cannot be assessed from the record.

Multiplicity arises when more than one outcome, comparison, subgroup, or analysis is tested. As a general statistical matter, conducting many tests can increase the chance of at least one apparently notable result unless the analysis plan accounts for that testing. The registry record does not report a multiplicity adjustment or a detailed plan specifying which analyses were primary, secondary, or exploratory. The single listed outcome and analysis do not establish whether other analyses were conducted but not posted.

Missing outcome data can affect a comparison if outcome availability differs between groups or relates to the likelihood of completion. The registry does not report the number of participants with missing primary-outcome data, reasons for missingness, follow-up completeness, or a missing-data method. The listed group counts should therefore be interpreted as posted counts, without assuming how missing observations were handled. No analysis population, such as an intention-to-treat population, is identified in the record.

The registry also does not report a protocol-level definition of the analysis population, exclusions after randomization, adherence, or whether participants were analyzed according to assigned group. These omissions limit assessment of how closely the posted comparison follows the randomized assignment. They do not demonstrate that data were missing or that analyses were not performed; those details are simply not reported in the registry record.

The absence of a detailed statistical plan also prevents assessment of whether the posted endpoint and analysis were selected before results were known. No interim analyses are reported. It would be inappropriate to infer that there were none, or to infer a particular plan for handling multiplicity or missing data, from the limited registry entries.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The adverse-event entries report zero serious events and zero other events in each listed group. The Minimal Intervention entry lists 145 participants at risk, and the Guided Intervention entry lists 117 at risk. Death counts are not reported. These entries are separate from the primary-outcome arm counts, which list 117 in Minimal Intervention and 145 in Guided Intervention. The difference in the group denominators across the outcome and adverse-event entries makes the safety figures difficult to reconcile with the randomized outcome groups.

The zero counts should be read as the registry’s posted adverse-event values, not as proof that no adverse events occurred outside the reporting framework or observation period. The registry does not report event definitions, collection procedures, follow-up duration for safety, or whether the at-risk counts represent all randomized participants. It also lists no serious adverse-event terms.

Because deaths are marked as not reported and the listed at-risk counts do not align with the outcome-group counts, the adverse-event entries offer limited information for comparing safety between groups. No conclusion about relative safety should be drawn from these sparse and internally difficult-to-reconcile entries.

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

The posted results describe a higher count of completed advance directives in Guided Intervention than in Minimal Intervention: 55 among 145 in the guided group and 15 among 117 in the minimal group. The recalculated unadjusted risk difference is 0.251, with a confidence interval from 0.152 to 0.351. The recalculated risk ratio and odds ratio also express a contrast favoring a higher recorded completion proportion in the guided group. The sponsor’s reported analysis gives an odds ratio of 4.16 and p < 0.05; because the record marks a discrepancy, that sponsor analysis takes precedence over the recalculation as the study’s own result.

The endpoint is completion of an advance directive, not whether participants later received care consistent with preferences or whether end-of-life care changed. Although the brief summary mentions those broader interests, the registry does not report a result for care delivered at the end of life. The completion finding cannot answer that separate question.

The result also does not establish how the intervention would perform in other settings or populations. The registry provides limited participant-characteristic information beyond the study’s focus on homeless persons, and it does not report intervention adherence or detailed follow-up. Generalizability therefore cannot be assessed fully from the record.

Randomization is an important design feature for comparing groups, but interpretation also depends on the details of allocation, outcome ascertainment, missing data, and analysis. Those details are not reported. The estimates describe the posted data and their statistical uncertainty; they do not resolve possible limitations arising from unreported study conduct or reporting decisions.

As a general statistical distinction, a small p-value is evidence against a specified null model under the test assumptions, not a measure of the outcome’s importance or a guarantee of causal validity. Likewise, an effect estimate is not a recommendation. The registry result is evidence about recorded advance-directive completion in this study, with limits on what can be inferred beyond that endpoint and comparison.

17. Why This Trial Matters Statistically

This study presents a statistical question that is more nuanced than comparing counts alone: how should a binary completion outcome be summarized, and how should uncertainty and reporting differences shape interpretation? A risk difference, risk ratio, and odds ratio all describe the contrast between the intervention groups, but each uses a distinct scale. Seeing those measures together helps distinguish absolute from relative descriptions without treating them as equivalent.

The comparison also illustrates why the sponsor’s analysis and a recalculation from posted summary statistics should be kept separate. The sponsor reports an odds ratio of 4.16 and p < 0.05, while the registry marks a discrepancy with the recalculated result. Giving precedence to the sponsor’s analysis respects the distinction between an official reported analysis and a simple unadjusted re-analysis. The unexplained discrepancy is itself relevant to statistical interpretation.

The endpoint has a clear practical subject: completion of an advance directive. Yet the study’s brief summary raises a broader question about care at the end of life, for which no outcome is posted. This distinction matters because a result on a process measure cannot be substituted for a result on subsequent care. Statistical conclusions should remain aligned with the outcome actually recorded.

Finally, sample-size illustrations based on the observed effect show how planning needs depend on the effect one aims to detect and the desired power. They do not reveal the study’s original rationale or provide observed power. The record’s incomplete reporting on missing data, analysis populations, and intervention delivery demonstrates why numerical estimates are only one part of evaluating a clinical study.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record is brief regarding study conduct. It does not report the eligibility criteria in detail, participant characteristics, recruitment procedures, allocation-sequence generation, or allocation concealment. It identifies a randomized, parallel design with no masking, but does not say whether outcome ascertainment was masked or how directive completion was verified. These gaps limit appraisal of selection, measurement, and implementation issues.

The primary endpoint is described as completion of an advance directive, but detailed criteria and follow-up procedures are not reported. The timeframe is 21 months, yet the record does not explain how incomplete follow-up or timing of completion was handled. It also does not report missing outcome counts, reasons for missingness, or the analysis population.

The group counts for the primary outcome list 117 in Minimal Intervention and 145 in Guided Intervention, while the adverse-event entries list at-risk counts of 145 for Minimal Intervention and 117 for Guided Intervention. The registry does not explain this difference. The sponsor-reported analysis and recalculated results are also marked as discrepant, without an explanation or a sponsor confidence interval. These are reporting limitations that should remain visible rather than be resolved by assumption.

The registry lists no secondary outcomes, although its brief summary mentions an interest in care given at the end of life. It does not report results for that broader question. Nor does the record provide detailed intervention-fidelity information, a statistical analysis plan, multiplicity procedures, interim analyses, or the original sample-size rationale. These details are not reported in the registry record; their absence from this record does not establish that they were absent from the study.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Intervention to Improve Expression of End of Life Preferences for Homeless Persons — NCT00546884.
• Registry record last updated 2017-07-13; status last verified 2017-06.
• Results first posted 2017-03-14.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT00546884 is a completed randomized, parallel-group behavioral study sponsored by the University of Minnesota. The registry lists an enrollment of 262, no masking, and study dates of 2007-11 to 2008-08 for start and primary completion. The study compares Minimal Intervention, involving an advance directive and written instructions, with Guided Intervention, involving an invitation to meet individually with a health care professional specializing in end-of-life care.

The sole listed primary outcome is completion of an advance directive within 21 months. The posted counts are 15 of 117 in Minimal Intervention and 55 of 145 in Guided Intervention. The sponsor reports a Chi-squared analysis with an odds ratio of 4.16 and p < 0.05. The registry marks a discrepancy with unadjusted recalculations, so the sponsor’s own analysis takes precedence. Further details about missing data, the analysis population, and the discrepancy are not reported in the registry record.