Post-chemotherapy Symptom Management SMART: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Post-chemotherapy Symptom Management SMART (NCT03494166), a randomized na study. The primary outcome is Symptom Severity Index- Comparison of Two Groups Created by First Randomization.

2. Clinical Question

3. Trial Design

This completed study, NCT03494166, is titled Post-chemotherapy Symptom Management SMART. The registry describes it as randomized, single-masked, and sequential, and its official title identifies a SMART design. It lists University of Arizona as sponsor, Cancer as the condition, and enrollment of 498. The recorded start date is 2018-07-01 and primary completion date is 2022-06-03.

The registry summary describes 451 survivors of solid tumors who had completed curative-intent chemotherapy within the past 2 years. They were interviewed at baseline and classified as high or low need for symptom management using comorbidity and depressive symptoms. High-need survivors entered the randomized intervention comparisons. In the first randomization, 282 received SMSH alone and 93 received SMSH plus TIPC. The primary outcome comparison is between these first-randomization groups.

The sequential design also included a second randomization. After 4 weeks of SMSH alone, participants who did not respond on depression were re-randomized to continue SMSH alone or add TIPC. The registry reports 30 in the continue-SMSH group and 31 in the add-TIPC group for the depressive-symptoms comparison created by this second randomization. That later comparison addresses a different decision point and a different group from the primary comparison; its results should not be treated as another estimate of the first assignment.

The low-need survivors served as a benchmark or follow-up group, with baseline and 13-week assessments and a brief week-4 symptom assessment. This benchmark is not the primary randomized comparison. The registry record does not report the original design’s sample-size justification, the masking procedures in detail, or a fuller account of the sequence of assignments beyond the summary and arm descriptions.

4. Participant Flow and Accounting

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

Before assignment: Of 500 consented individuals, 451 had a baseline interview, 71 were low need, 375 were high need and entered into randomization. Five participants were found ineligible. Three participants in the high need group dropped out after baseline before the first randomization. Three participants in the low need group were misclassified initially as high need and were randomized, resulting in 375 randomized and 68 continuing as low need without interventions.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Of the 375 high-need survivors initially randomized, 282 received the Symptom Management and Survivorship Handbook (SMSH) alone and 93 received Telephone Interpersonal Counseling (TIPC) + SMSH.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Of 500 individuals who consented, 451 completed a baseline and 5 were ineligible.

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Symptom Severity Index- Comparison of Two Groups Created by First Randomization, measured over Weeks 1-13.

The primary endpoint is the Symptom Severity Index, a continuous score based on the modified General Symptom Distress Scale. It assesses the severity of 18 symptoms, but the index excludes depression and sums the other 17 symptoms. The assessed symptoms include fatigue, sleep difficulties, pain, headache, difficulty concentrating, appetite problems, nausea, vomiting, constipation, diarrhea, numbness or tingling, skin problems, swelling, weakness, shortness of breath, cough, and anxiety. Respondents rate symptom severity from 0, not present, to 10, worst possible. The index can range from 0-170, with higher scores indicating worse symptom severity.

The primary summary averages the index over weeks 1-13, drawing on weekly contacts, baseline, and 13-week interviews. A combined symptom-burden measure can represent the overall severity of several symptoms rather than focusing on one complaint. That makes it relevant to a symptom-management intervention aimed at survivors experiencing multiple symptoms. The registry says the symptom collection does not form a scale, so internal consistency reliability was not applicable. The posted arm values are least-squares means with standard errors; they are not individual-level scores or simple counts of symptoms.

7. Results Posted in the Registry

• High Need B: Start With SMSH+TIPC: mean 25.86 versus 24.53 on control; difference 1.33 (95% CI -1.29 to 3.95), standardized effect d = 0.12; z-test p = 0.319.

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.

Depressive Symptoms- Comparison of Two Groups Created by First Randomization.

• 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 errors.
• Result:
  • High Need B-TIP-C+SMSH: mean 12.30 versus 11.89 on control; difference 0.41 (95% CI -1.81 to 2.63), standardized effect d = 0.04; z-test p = 0.717.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between High Need B-TIP-C+SMSH and the control. The interval gives the range of effects that remain compatible with the data.

Depressive Symptoms - Comparison of Two Groups Created by Second Randomization

• 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 errors.
• Result:
  • Add TIPC to SMSH After Week 4: mean 16.81 versus 16.05 on control; difference 0.76 (95% CI -4.84 to 6.36), standardized effect d = 0.07; z-test p = 0.790.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Add TIPC to SMSH After Week 4 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results follow a broadly similar pattern to the primary result: neither randomization comparison shows a clear separation in average depressive-symptom scores, and the reported uncertainty includes no difference. The secondary analyses concern depressive symptoms at week 13, rather than the primary symptom-severity index averaged over weeks 1-13. One comparison follows the first randomization; the other concerns participants re-randomized after 4 weeks of SMSH alone for non-response on depression.

These endpoints add context about a distinct symptom domain and, in the second randomization, a later treatment decision. They do not change what the primary endpoint measures or make the primary estimate more precise. The two secondary comparisons also involve different randomization stages and populations, so they should not be collapsed into one overall treatment contrast. The result from the second randomization is especially tied to the group eligible for that re-randomization, rather than to all high-need survivors.

Unadjusted secondary results carry less weight as confirmatory evidence when several outcomes or comparisons are examined. General statistical context: making multiple tests increases the chance that at least one result will look notable by chance, unless the analysis plan accounts for multiplicity. The registry record does not report a multiplicity adjustment or a hierarchy specifying how the secondary endpoints should be interpreted. Their estimates can therefore be read as exploratory or supportive descriptions, not as independent confirmation of a treatment effect. The overall pattern is compatible with the primary result’s uncertainty, but it does not establish equivalence or rule out effects that the studies could not estimate precisely.

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

• Depressive Symptoms- Comparison of Two Groups Created by First Randomization.
• Depressive Symptoms - Comparison of Two Groups Created by Second Randomization

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a score whose values express symptom severity rather than a count of events. The registry reports least-squares means and standard errors for each arm. A least-squares mean is a model-based group mean; the record does not describe the covariates or other details needed to reconstruct how those means were obtained. The standard error describes the precision of an estimated mean, not the spread of individual participants’ scores.

What does the reported mean difference represent?

The sponsor reports a mixed-model analysis of final values, with a mean difference of -1.31. A mean difference expresses a contrast between group averages in the score’s original units. Its sign depends on the order used for the contrast. The registry lists the groups in an order but does not explain the sign convention for the sponsor’s estimate. The posted arm means, considered as SMSH plus TIPC minus SMSH alone, yield an unadjusted recalculated difference of 1.33. The sponsor estimate and the recalculation therefore have similar absolute sizes but opposite signs; the record does not explain this orientation difference.

Why are the recalculated and sponsor results not identical?

The recalculation uses posted summary statistics to form a simple, unadjusted comparison. It is not a reproduction of the sponsor’s mixed model. The sponsor analysis is described as a mixed-model analysis, while the recalculation uses the arm means and their reported standard errors. These approaches can produce different estimates and confidence intervals because they use different statistical information and assumptions. The record does not provide enough model detail to identify the source of each difference. The recalculated p-value is .319; the sponsor reports p = .31. Their closeness should not be taken as proof that the analyses are identical.

What does a confidence interval convey?

A confidence interval gives a range of estimates compatible with the data and the method used to calculate it. It reflects uncertainty in the estimated group difference. The primary recalculated interval runs from -1.289 to 3.949; the sponsor-reported interval runs from -3.90 to 1.25. Both include zero, the value corresponding to no mean difference. This means the estimates are not precise enough to rule out either direction of difference. A confidence interval is not a guarantee that the true effect lies in the interval, and it does not indicate the probability that a particular treatment effect is true.

What does the p-value tell the reader?

A p-value describes how unusual results at least as inconsistent with a specified null hypothesis would be under the assumptions of the statistical test. It is not the probability that the null hypothesis is true, nor does it measure the clinical importance of a difference. The recalculated p-value is unadjusted, and the sponsor reports p = .31 for the primary analysis. Neither value, by itself, establishes equivalence or proves that the observed difference is meaningful. Interpretation should consider the estimated difference and its interval as well as the test result.

Why can symptom scores be hard to summarize?

The index combines ratings across 17 symptoms, and the registry notes that this collection does not form a scale. A single average can make the overall burden easier to compare, but it can conceal variation among symptoms and among participants. A group mean does not indicate whether changes were concentrated in one symptom or spread across several. Nor does it describe the range of individual experiences. The registry’s statement that internal consistency reliability was not applicable is consistent with treating this index as a sum of symptom severities, rather than assuming the symptoms are interchangeable items measuring one underlying scale.

Why might over-dispersion matter generally?

General statistical context: over-dispersion occurs when observed variability is greater than a model expects. It is especially relevant for count outcomes, where an overly narrow variance assumption can make standard errors and confidence intervals too small. The primary endpoint is a continuous symptom score, and the record does not report an over-dispersion assessment. It would therefore be inappropriate to claim that over-dispersion was present or to attribute uncertainty in this result to it. The broader lesson is that uncertainty estimates depend on whether the model’s assumptions describe the observed data.

The registry identifies the primary sponsor method but does not report its full model specification, diagnostic checks, missing-data procedures, or analysis-population definition. These details matter when assessing model-based estimates. In their absence, the sponsor’s reported result can be described as posted, while the summary-statistic recalculation should be understood as a separate, unadjusted illustration.

11. Confidence Intervals and Precision

The primary estimate is imprecise enough that its direction is uncertain. The recalculated mean difference is 1.33, with a 95% confidence interval from -1.289 to 3.949. That interval includes zero and extends to both a lower symptom score and a higher symptom score for the group starting with SMSH plus TIPC, when the contrast is read as that group minus SMSH alone. Its width indicates that the posted summary statistics do not pin down a narrow range of plausible differences.

The sponsor-reported 95% confidence interval is -3.90 to 1.25, also spanning zero. Its negative sign contrasts with the positive sign of the recalculated B-minus-A estimate. The record does not explain the contrast orientation, so direction should be interpreted from the arm means when describing that particular unadjusted contrast, and the sponsor estimate should be quoted with its reported sign. The two intervals differ in their endpoints, reflecting that the reported sponsor model and the simple recalculation are not the same analysis.

A confidence interval that includes zero does not demonstrate that the treatments have the same effect. It indicates that the data and analysis do not rule out no difference at the interval’s stated confidence level. The interval also permits differences on either side of zero, so a conclusion about direction would be too strong. The registry record does not report a threshold for a clinically important difference; statistical precision alone cannot determine whether any particular value in the interval would matter to survivors.

The arm standard errors are 0.68 for SMSH alone and 1.15 for SMSH plus TIPC. These describe uncertainty around the reported arm means, not the amount of variation among individual symptom scores. The group sizes differ, and the estimates come from the posted analysis; precision should be judged from the comparison interval rather than by reading the arm standard errors as individual variability. The record does not report additional information about missingness that would clarify whether the observed precision fully reflects uncertainty from incomplete follow-up.

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 participants per arm, not total participants, because the outcome is continuous rather than time-to-event. The registry’s planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as its reference and considers detecting the stated fraction of that effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm estimated to give an 80% chance of detecting the specified effect under those planning assumptions, if that effect were the true effect and the assumptions held. The 90% power column uses a higher target chance of detection and therefore generally requires more participants per arm. These columns are planning illustrations, not observed power: they do not measure the probability that the completed trial detected an effect, and they do not change the interpretation of its confidence interval.

The rows use different fractions of the observed effect. Planning to detect a smaller effect requires more participants per arm, because a smaller difference is harder to distinguish from random variation. The reported figures are conditional on the observed effect and the listed assumptions; they are not a recommendation or a reconstruction of the study’s original design. The sample-size curve should be read in the same planning context: it represents how the projected requirement changes as the target effect changes, rather than displaying an additional trial result.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 1.330; pooled standard deviation σ = 11.339.
2. n = 2 × (1.96 + 0.842)² × 11.339² / 1.330² = 1,141.0, rounded up to 1,141 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
delta <- 1.33                      # observed difference in means
sigma <- 11.3388949345958                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3494166)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 1,141 (80% power), 1,528 (90% power)
 75% of observed effect: n per arm = 2,029 (80% power), 2,716 (90% power)
 50% of observed effect: n per arm = 4,564 (80% power), 6,110 (90% power)
power.t.test: 1141.9 
Simulated power at n = 1,141 per arm: 0.798 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis is reported as a mixed-model analysis of final values. It gives a mean difference of -1.31, a 95% confidence interval from -3.90 to 1.25, and p = .31. These are the registry’s formal reported inferential results for the primary comparison. The registry does not provide the model specification, so additional adjustment details should not be inferred.

The separate recalculation uses posted group means and standard errors to estimate an unadjusted difference of 1.33, with a 95% confidence interval from -1.289 to 3.949 and p = 0.319. It is a summary-statistic calculation, not a re-fit of the sponsor’s model. The point estimates have similar absolute sizes but opposite signs. The registry does not explain the contrast orientation; the arm means themselves are higher for the group starting with SMSH plus TIPC.

The sponsor interval and recalculated interval both include zero, and the p-values are close. Their endpoints are not identical, which is expected when comparing a model-based analysis with a simple unadjusted recalculation. The recalculation is useful for checking the scale and broad pattern of the posted result, but it should not replace the sponsor’s stated analysis or be presented as if it reproduces that analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 4 outcome measures and 4 analyses, and it details two secondary depressive-symptom comparisons in addition to the primary symptom-severity comparison. The outcomes address different questions, including the first randomization and the later re-randomization. Considering several outcomes and comparisons can increase the chance of a seemingly unusual result arising by chance. General statistical methods for addressing this include prespecifying a primary outcome, using a testing hierarchy, or adjusting the interpretation of multiple tests.

Whether any such approach was used is not reported in the registry record. No multiplicity adjustment is described for the posted secondary results. The p-values should therefore be interpreted as reported for their individual analyses, not as controlling the overall chance of a false positive across all outcomes. The registry’s description of the primary outcome helps identify the main comparison, but does not establish what testing hierarchy or decision rules governed the study.

The record also does not report how missing outcome data were handled, how many participants contributed data at each assessment, or whether sensitivity analyses assessed the effect of missingness. The outcome collection drew on baseline, weekly contacts, and 13-week interviews, but that schedule alone does not establish that all assessments were completed or explain how incomplete observations entered the analysis. Missingness can affect both the estimate and its precision, particularly if participants with missing data differ systematically from those with observed data.

The analysis population is not reported in enough detail to determine whether the sponsor used an intention-to-treat population, a per-protocol population, or another definition. The initial randomized group sizes are described, but those counts do not by themselves establish who was included in every endpoint analysis. The registry record also does not report adherence summaries or detailed handling of participants who changed or did not receive their assigned intervention. These omissions limit assessment of the relationship between random assignment, treatment received, and the reported estimates.

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 serious adverse events for the low-need benchmark or follow-up group, the high-need SMSH or TIPC group, and the high-need TIPC-plus-SMSH group. The recorded numbers at risk are 71, 282, and 93, respectively. Serious adverse events affected 0 participants in each listed group. Other adverse events also affected 0 in each group. The registry records deaths of 0, 1, and 3 for those groups, respectively.

These are descriptive registry counts. The record does not report the adverse-event observation period, event definitions, relationship to the intervention, or further details about the deaths. The groups also represent different study roles, including a low-need benchmark and high-need randomized groups, so the counts should not be treated as a direct randomized comparison of safety. A zero recorded count does not show that an event is impossible or establish that an intervention is free of risk; it states only what the registry reports for these categories.

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

The primary posted results describe average symptom severity among high-need survivors randomized to start with SMSH alone or SMSH plus TIPC. The group means are close in scale, and both the sponsor-reported confidence interval and the unadjusted recalculated interval include zero. The evidence therefore does not establish a clear difference in the primary outcome between the initial strategies. The estimates also do not establish that the strategies are equivalent: the intervals allow for differences in either direction, and the registry gives no threshold for deciding what difference would be clinically important.

The endpoint is an average symptom index over weeks 1-13, not a direct measure of every aspect of survivorship or of a single symptom. A similar average can arise from different patterns across individual symptoms and participants. The results do not show which symptoms changed, whether particular participants benefited more, or whether the intervention affected outcomes not reported in the registry. They also do not establish the effect of adding TIPC after week 4 among non-responders; that is a separate question addressed by the second randomization and its depressive-symptom endpoint.

The findings apply to the trial’s described high-need population and intervention sequence. The low-need benchmark group was followed, but it is not the randomized comparator for the primary result. The comparison should not be generalized automatically to all cancer survivors, people who did not complete curative-intent chemotherapy, or other care settings. The registry’s description and posted results do not support conclusions about outcomes outside the measured period, longer-term effects, or specific subgroups.

Finally, statistical uncertainty is only one part of interpretation. The registry does not report a clinically important difference threshold, detailed missing-data procedures, or the full model specification. Those gaps make it difficult to judge whether the observed estimates are sufficiently precise for a particular practical decision. The results are best read as estimates with substantial uncertainty, rather than as proof that one starting strategy is preferable or that no meaningful difference exists.

18. Why This Trial Matters Statistically

This trial is statistically informative because it uses a sequential randomized design to study intervention decisions at more than one point in symptom management. The first randomization compares starting with SMSH alone against starting with SMSH plus TIPC. A later randomization addresses whether to continue SMSH alone or add TIPC after an inadequate depression response. Those are distinct questions, and keeping them separate is essential to interpreting the estimates.

The primary endpoint also illustrates the difference between a group average and the experience of individual participants. A summed index can provide a compact summary of multiple symptoms, but it cannot show which symptoms account for the result or whether participants respond differently. The registry explicitly notes that the set of symptoms does not form a scale, making it important not to overstate what the score represents.

The comparison is a useful example of why a non-significant result is not evidence of equivalence. The primary confidence intervals include zero but also allow differences in either direction. Precision, rather than a p-value alone, shows why the direction and size of a potential difference remain uncertain. The sponsor’s model-based estimate and the unadjusted recalculation also illustrate why a recalculation from summary statistics should not be confused with the study’s stated analysis.

Finally, the registry record leaves important reporting questions unresolved, including missing-data methods, multiplicity, the analysis population, and the original sample-size rationale. These are not minor technicalities: they shape how confidently estimates can be interpreted. The trial therefore matters as a case study in reading a sequential design, distinguishing endpoints and assignment stages, and treating uncertainty and incomplete statistical reporting carefully.

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 primary comparison is limited to high-need survivors in the first randomization. The low-need group was a benchmark or follow-up group, not the randomized comparator for the primary outcome. Consequently, the primary result cannot be read as a randomized comparison between high-need and low-need survivors. The second randomization addresses a selected group of participants who did not respond on depression after 4 weeks of SMSH alone, so its results apply to a different decision point and population.

The registry provides limited detail about the intervention and outcome-analysis procedures. It describes the handbook, weekly calls, and counseling topics, but does not report a detailed account of adherence or intervention fidelity. The sponsor’s mixed-model specification, covariates, diagnostics, and missing-data handling are not reported in the registry record. The analysis population for each outcome is also not defined in detail. These gaps make it difficult to assess how robust the estimates are to modeling and incomplete follow-up.

The symptom index combines 17 symptoms and excludes depression, while the secondary outcomes focus on depressive symptoms. The registry says the symptom collection does not form a scale, and it does not report symptom-specific results in the registry record described. An overall score may therefore conceal different patterns across symptoms. The record also does not report a threshold for a clinically important difference, limiting interpretation of whether values within the confidence intervals would be meaningful to participants.

Further limits include the absence of a reported multiplicity plan, the lack of detailed safety-event timing and definitions, and the absence of the trial’s original sample-size justification. The registry records a single-masked design but does not describe masking procedures in detail. These limitations do not invalidate the posted estimates, but they constrain what can be concluded about their precision, robustness, and scope.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Post-chemotherapy Symptom Management SMART — NCT03494166.
• Registry record last updated 2023-10-19; status last verified 2023-09.
• Results first posted 2023-10-19.
• 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

NCT03494166 is a completed randomized, single-masked, sequential study of post-chemotherapy symptom management. The primary comparison is among high-need survivors randomized to start with SMSH alone or SMSH plus TIPC. The endpoint is an average symptom-severity index over weeks 1-13, with higher scores indicating worse symptoms.

The posted arm means are 24.53 and 25.86. The sponsor reports a mixed-model mean difference of -1.31, with a 95% confidence interval from -3.90 to 1.25 and p = .31. The unadjusted recalculation is 1.33, with a 95% confidence interval from -1.289 to 3.949 and p = 0.319; the registry does not explain the opposite sign orientation. Both intervals include zero and leave uncertainty about the direction and size of any difference.

The registry also reports two secondary depressive-symptom comparisons and descriptive adverse-event counts. Multiplicity procedures, missing-data methods, analysis populations, and the original sample-size rationale are not reported in the registry record.