A Study to Assess the Effect of Oral Temanogrel on Digital Blood Flow in Adult Participants With Raynaud's Phenomenon Secondary to Systemic Sclerosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Assess the Effect of Oral Temanogrel on Digital Blood Flow in Adult Participants With Raynaud's Phenomenon Secondary to Systemic Sclerosis (NCT04915950), a randomized phase 2 study. The primary outcome is Change in Digital Blood Flow Based on Rewarming Area Under the Curve (AUC) During Thirty Minutes Following a Cold Challenge.

2. Clinical Question

The clinical question centers on a measured physiological response rather than a reported symptom outcome. Participants' hands were immersed in a temperature-controlled water bath for one minute, after which skin temperature was assessed for 30 minutes. Infrared thermography was used as an indirect measure of blood flow, and the primary outcome was the area under the rewarming curve.

The study record describes two temanogrel doses, 120 mg and 60 mg, and a placebo condition. The available arm summaries give mean primary-outcome values for each condition. The comparison estimates are unadjusted recalculations from those summaries, rather than results from a reported crossover analysis. Because the design is crossover, the relationship between measurements from the same participant could matter to an analysis; the registry record does not report an analysis accounting for that relationship.

This is a Phase 2 study that the registry marks as terminated. Its recorded enrollment is 13. These design and enrollment details frame how much information the posted results can provide; they do not establish why the study ended or how its original sample size was chosen. Those explanations are not reported in the registry record.

3. Trial Design

The study is identified as Phase 2, multicenter, randomized, double-blind, placebo-controlled, and crossover. It compared oral temanogrel with placebo in adults with Raynaud's phenomenon secondary to systemic sclerosis. The registry lists temanogrel 120 mg, temanogrel 60 mg, and placebo in the posted outcome summaries.

A crossover design means that participants can receive more than one study condition over time, with each participant potentially contributing measurements under multiple conditions. This differs from a design in which each participant is assigned to only one treatment group. The registry record does not report the treatment sequence, period structure, duration of treatment, washout arrangements, or whether those features differed between the listed Stage A and Stage B arms. The Stage A and Stage B arm descriptions are not reported in the registry record.

The record lists enrollment of 13 and status as terminated. It gives a start date of 2021-11-03 and a primary completion date of 2022-09-02. These record details do not identify the reason for termination, whether the planned study procedures were completed, or whether all randomized participants contributed outcome data. Those details are not reported in the registry record.

The primary analysis population is described as the full analysis set, including all randomized participants irrespective of whether they received any study treatment. The posted primary arm summaries each list 13 participants. However, the statistical analysis used for the crossover design, including any adjustment for within-participant correlation, treatment period, or sequence, is not reported in the registry record. No reported analyses are listed for the secondary outcomes either.

In the registry record, the primary outcome is a continuous measure summarized by a mean and standard deviation. The posted comparisons give mean differences against placebo and confidence intervals. These comparisons are unadjusted recalculations from arm-level summary statistics and should not be confused with a reported analysis of the randomized crossover trial. The original statistical plan and sample-size justification are not reported 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.

Before assignment: A total of 13 participants were enrolled and randomized in the study.

Stage A: Treatment Period 1 (1 Day)

Stage A:Washout Period(72hours to 7days)

Stage A: Treatment Period 2 (1 Day)

Stage A:Washout Period(72hours to 7days)

Analysis population for the primary outcome, as defined in the registry: FAS included all randomized participants, irrespective of whether they received any study treatment.

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: The full analysis set (FAS) included all randomized participants, irrespective of whether they received any study treatment.

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Change in Digital Blood Flow Based on Rewarming Area Under the Curve (AUC) During Thirty Minutes Following a Cold Challenge, measured over 30 minutes following a cold challenge.

The primary endpoint was change in digital blood flow based on rewarming area under the curve during 30 minutes following a cold challenge. It is reported in degrees Celsius*seconds and summarized as a mean with a standard deviation. The outcome represents the area under the skin-temperature curve during rewarming after the cold challenge.

In the procedure described in the registry, participants' hands were immersed in a temperature-controlled water bath at 15 [+/- 1] degree celsius for one minute. Digital blood flow was then assessed for 30 minutes. Infrared thermography measured skin temperature and was described as an indirect method for evaluating blood flow. The primary result was based on the average across the eight assessed fingers: left and right index, middle, ring, and little fingers.

As a general statistical concept, an area under the curve can capture both the level and the course of a measured response across a period of observation, rather than describing only a single measurement. Here, the endpoint was used to represent rewarming after cooling, with skin temperature serving as the recorded signal. The registry description also calls rewarming a delicate phase of therapeutic hypothermia; how that wording relates to this study's assessment is not explained in the registry record.

This endpoint is a physiological measure, not a direct measure of symptoms or daily functioning. Its interpretation is limited to the measurement approach and observation period described in the record. The registry does not report a threshold for a meaningful change in the endpoint.

7. Results Posted in the Registry

• Temanogrel 120 mg: mean 43,912 versus 44,530 on control; difference -618.00 (95% CI -5,633 to 4,397), standardized effect d = -0.09; z-test p = 0.809.
• Temanogrel 60 mg: mean 44,000 versus 44,530 on control; difference -530.00 (95% CI -5,799 to 4,739), standardized effect d = -0.08; z-test p = 0.844.

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.

Maximum Reduction in Temperature Following a Cold Challenge Assessed With Infrared (IR) Thermography

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Temanogrel 120 mg: mean 23.06 versus 22.45 on control; difference 0.61 (95% CI -0.99 to 2.21), standardized effect d = 0.29; z-test p = 0.455.
  • Temanogrel 60 mg: mean 22.77 versus 22.45 on control; difference 0.32 (95% CI -1.37 to 2.01), standardized effect d = 0.15; z-test p = 0.711.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Temanogrel 120 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Temanogrel 60 mg and the control. The interval gives the range of effects that remain compatible with the data.

Maximum Reduction in Perfusion Temperature Following a Cold Challenge With Laser Speckle Contrast Imaging (LSCI)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Temanogrel 120 mg: mean 33.67 versus 36.04 on control; difference -2.37 (95% CI -29.76 to 25.02), standardized effect d = -0.07; z-test p = 0.865.
  • Temanogrel 60 mg: mean 30.77 versus 36.04 on control; difference -5.27 (95% CI -32.43 to 21.89), standardized effect d = -0.15; z-test p = 0.704.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Temanogrel 120 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Temanogrel 60 mg and the control. The interval gives the range of effects that remain compatible with the data.

Maximum Recovery in Temperature Following a Cold Challenge Assessed With IR Thermography

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Temanogrel 120 mg: mean 25.11 versus 25.76 on control; difference -0.65 (95% CI -3.82 to 2.52), standardized effect d = -0.16; z-test p = 0.688.
  • Temanogrel 60 mg: mean 25.38 versus 25.76 on control; difference -0.38 (95% CI -3.75 to 2.99), standardized effect d = -0.09; z-test p = 0.825.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Temanogrel 120 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Temanogrel 60 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists 15 secondary outcomes, including temperature and perfusion measures assessed after a cold challenge with infrared thermography and laser speckle contrast imaging. The posted results include numerical summaries and comparisons for several of these measures. Across those summaries, estimates vary in direction and the intervals are broad; the reported intervals for the detailed comparisons span zero. This overall pattern does not provide a clear, precise secondary signal that changes the reading of the primary result.

The secondary measures relate to the primary question because they describe other aspects of the temperature or perfusion response to cooling and rewarming. They are not identical to the primary rewarming area under the curve: some describe maximum reduction, maximum recovery, early area under the curve, or early slope, and they use different measurement approaches. They can add physiological context, but they do not replace the primary endpoint or establish an effect on symptoms or functioning.

The registry record lists no reported secondary analyses. The numerical comparisons available in the posted summaries are unadjusted recalculations, and their statistical interpretation should be cautious. Examining many outcomes creates multiple opportunities for apparently notable findings to arise by chance. As a general statistical principle, unadjusted results across multiple outcomes carry less weight than a prespecified analysis that addresses multiplicity.

The record does not report a multiplicity strategy, such as a hierarchy among outcomes or an adjustment to account for multiple comparisons. Without that information, the secondary results are best viewed as exploratory descriptions. Their variability and uncertainty do not resolve the imprecision in the primary comparison, and no single secondary measure should be treated as confirmatory on the basis of these unadjusted comparisons.

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

• Maximum Reduction in Temperature Following a Cold Challenge Assessed With Infrared (IR) Thermography
• Maximum Reduction in Perfusion Temperature Following a Cold Challenge With Laser Speckle Contrast Imaging (LSCI)
• Maximum Recovery in Temperature Following a Cold Challenge Assessed With IR Thermography
• Maximum Recovery in Perfusion Temperature Following a Cold Challenge Assessed With LSCI
• AUC During the Initial Two Minutes Following a Cold Challenge Assessed With IR Thermography
• Perfusion AUC During the Initial Two Minutes Following a Cold Challenge Assessed With LSCI
• Slope During the Initial 2 Minutes (120 Seconds) Following a Cold Challenge Assessed With IR Thermography
• Perfusion Slope During the Initial 2 Minutes (120 Seconds) Following a Cold Challenge Assessed With LSCI

9. Statistical Interpretation

10. Statistical Methods Explained

The primary measure is continuous: it represents rewarming area under the curve and is reported as a mean and standard deviation. The posted means describe the average recorded outcome in each listed condition. A standard deviation describes variation among observations around a mean; it is not the same as the uncertainty in the mean or the uncertainty in a treatment comparison.

What does a mean difference describe?

A mean difference compares the average outcome in one condition with the average in the reference condition. In the posted primary comparisons, placebo is the reference. A negative estimate means the temanogrel arm's posted mean is lower than the placebo mean on this outcome's scale; it does not by itself establish a meaningful or reliable difference. The two primary recalculated estimates are -618 for temanogrel 120 mg and -530 for temanogrel 60 mg.

These comparison estimates are unadjusted recalculations from posted summary statistics. They use the arm means and standard deviations to estimate a difference and its uncertainty. They are not identified as the sponsor's analysis, and no sponsor analysis is reported in the registry record. In particular, the calculations do not use the participant-level pairing that may be relevant in a crossover design.

What does a confidence interval add?

A confidence interval expresses uncertainty around an estimate. As a general statistical explanation, a confidence interval is a range of values that are reasonably compatible with the data and the method used to construct it. Wider intervals indicate less precision than narrower intervals. The primary intervals, -5633 to 4397 for temanogrel 120 mg and -5799 to 4739 for temanogrel 60 mg, include zero. That means the recalculated comparisons do not precisely separate a negative difference from no difference or a positive difference.

A confidence interval is not a guarantee that the true value lies in the interval, nor does it state the probability that a particular treatment effect is correct. Its interpretation depends on the analysis method and assumptions. Here the recalculated intervals are unadjusted and should be read as descriptive inferential summaries, not as a replacement for an analysis specified for the crossover trial.

How should the p values be read?

The unadjusted p values are 0.809 for the 120 mg comparison and 0.844 for the 60 mg comparison. As a general statistical concept, a p value describes how unusual data at least as incompatible with a specified no-difference model would be if that model and the analysis assumptions held. It is not the probability that the no-difference model is true, and it does not quantify the size or clinical importance of an effect. These p values come from the unadjusted recalculations and are not reported registry analyses.

The record does not describe a prespecified statistical model, treatment-period adjustment, sequence adjustment, or handling of within-participant correlation. Such details matter in a crossover study because observations from one participant can be related across treatment conditions. General statistical reasoning suggests that ignoring this relationship can affect the uncertainty attached to a comparison. The precise effect cannot be determined from arm-level means and standard deviations alone.

Why does variation matter?

Variation is substantial relative to the precision of the reported comparisons, as reflected in their broad intervals. In general, greater variability makes it harder to estimate a mean difference precisely when the amount of information is limited. The standard deviations are descriptive summaries of spread; they do not reveal whether the data were skewed, whether there were unusual observations, or how the within-person differences were distributed. Those features are not reported in the registry record.

The primary outcome averages measurements across eight fingers for each participant, as described in the record. That aggregation defines the posted measure, but individual finger-level summaries and the exact participant-level calculation are not reported. Readers should therefore interpret the reported endpoint as the registry-defined summary, rather than infer details about the measurements from each finger.

Overall, the posted mean differences, intervals, and p values are useful for describing the size and imprecision of simple comparisons. They do not convey a complete analysis of a randomized crossover trial. The registry record does not report the original analysis plan, the original sample-size justification, interim analyses, or a sponsor inferential analysis. No extra assumptions about those elements can be inferred from the recalculations.

11. Confidence Intervals and Precision

The primary comparisons have broad confidence intervals relative to their point estimates. For temanogrel 120 mg, the mean difference was -618 and the 95% confidence interval ranged from -5633 to 4397. For temanogrel 60 mg, the mean difference was -530 and the 95% confidence interval ranged from -5799 to 4739. Both intervals span zero, so the estimates are compatible with no mean difference as well as with differences in either direction under the recalculation method.

As a general statistical explanation, an interval's width reflects precision: a narrower interval conveys a more precise estimate than a wider one. The posted intervals do not pin down the primary mean difference closely. The registry record does not report a threshold that would distinguish a clinically important difference from a difference of little importance, so the intervals cannot be classified against such a threshold.

Precision is affected by the amount of information and the variability in the data. The posted primary summaries list 13 participants for each condition, and the standard deviations are reported for each arm. In a crossover trial, the correlation between measurements from the same participant can also inform precision. That correlation is not available in the arm-level summaries, and the recalculations do not account for it.

The intervals should therefore be read as uncertainty around unadjusted comparisons of posted summaries, not as precision estimates from a reported crossover model. The primary results are not sufficiently precise to establish a narrow range for the underlying contrast. That uncertainty is distinct from whether the point estimate is positive or negative.

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 of the participant counts that a hypothetical two-arm study might require under stated assumptions. For these continuous outcomes, the figures are participants per arm, not a total across arms and not total events. The registry record's own original design assumptions and sample-size justification are not reported.

The illustration assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It uses the observed effect as a starting point, then also considers planning for 75% and 50% of that observed effect. The 80% power column represents the number of participants per arm under those assumptions for a design with an 80% chance of detecting the specified effect if that effect were the true one. The 90% column expresses the corresponding planning target for a 90% chance.

Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm when the target is a smaller fraction of the observed effect. This relationship is a general feature of statistical planning, not evidence that the trial was designed using these figures. The observed effects come from this small study's posted summaries and may not be stable estimates for future planning.

These values are planning illustrations, not observed power. They do not describe what power the completed study had, and they do not correct for the crossover design or replace a design-specific calculation. The registry record does not report whether these assumptions match the study's original planning.

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 = -618.000; pooled standard deviation σ = 6523.725.
2. n = 2 × (1.96 + 0.842)² × 6523.725² / -618.000² = 1,749.3, rounded up to 1,750 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 <- -618                      # observed difference in means
sigma <- 6523.72472633541                     # 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(4915950)
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 = 1,750 (80% power), 2,342 (90% power)
 75% of observed effect: n per arm = 3,110 (80% power), 4,164 (90% power)
 50% of observed effect: n per arm = 6,998 (80% power), 9,367 (90% power)
power.t.test: 1750.2 
Simulated power at n = 1,750 per arm: 0.802 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary outcome and multiple secondary outcomes, but it does not report how the analysis accounted for testing more than one outcome or more than one treatment comparison. A multiplicity strategy is not reported in the registry record. This matters because examining many outcomes can increase the chance of seeing an apparently unusual result even when there is no underlying treatment difference. As a general statistical concept, adjustment or a prespecified testing hierarchy can help control that risk; the record does not say whether either was used.

The posted comparisons are unadjusted recalculations from summary statistics. Their p values should not be treated as multiplicity-adjusted evidence, and no adjustment has been added to these explanations. The registry lists no reported analyses for the secondary outcomes. The original statistical analysis plan, including any planned outcome hierarchy or interim analyses, is not reported in the registry record.

The analysis population is described as the full analysis set, including all randomized participants regardless of whether they received study treatment. That definition is reported, but the registry does not state how missing outcome measurements were handled, whether all randomized participants had evaluable primary data, or whether any imputation was used. The record's enrollment and posted arm counts do not establish the completeness of outcome follow-up.

Missing-data handling is especially relevant when interpreting an outcome observed after a cold challenge and across a defined assessment period. The registry record does not describe reasons for missing measurements, exclusions from particular analyses, sensitivity analyses, or methods used to address missing data. These omissions limit assessment of potential bias.

The record also does not report a crossover-specific analysis, including adjustment for treatment period, sequence, or within-participant correlation. It does not report the original statistical plan, sample-size justification, or interim-analysis plan. Those items should be considered unknown rather than assumed to have followed a particular method.

15. 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.

Most frequent non-serious adverse event terms

The registry reports serious adverse events for 13 participants at risk in each of the three listed conditions: temanogrel 120 mg, temanogrel 60 mg, and placebo. The number of participants with a serious adverse event was 0 in each condition. The registry also lists 0 deaths in each condition. No serious adverse-event terms are listed.

For other, non-serious adverse events, the posted counts are 4 with temanogrel 120 mg, 3 with temanogrel 60 mg, and 6 with placebo, with 13 participants at risk in each condition. These are reported counts, not an analysis of comparative risk. The registry record does not provide event types or a statistical comparison in the safety data.

In a crossover study, participants may contribute to more than one treatment condition, so condition-level counts should not be read as counts of separate groups of people. The registry record does not provide enough detail to determine timing, exposure duration, recurrence, or the relationship of individual events to treatment periods. Zero reported serious events in these summaries does not establish that serious events cannot occur, and the counts should be interpreted in light of the study's limited enrollment.

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

The results describe a small randomized crossover study of oral temanogrel and placebo in adults with Raynaud's phenomenon secondary to systemic sclerosis. The primary outcome was an indirect physiological measure: skin-temperature rewarming after a cold challenge, summarized as area under the curve over 30 minutes. The posted mean differences for both temanogrel doses were negative, while their unadjusted confidence intervals included zero and were broad.

This means the simple comparisons do not precisely identify the direction or size of a primary difference. They do not establish equivalence, and they do not prove that a difference is absent. Nor do they establish a treatment benefit or lack of benefit. The interval estimates describe uncertainty in the unadjusted recalculations, not a reported sponsor analysis that accounts for the crossover design.

The endpoint is not itself a symptom measure, and the registry record does not report a threshold for a meaningful change in this physiological outcome. Thus, even a precise difference in the measured endpoint would not automatically establish a change in symptoms or daily functioning. The results should be kept within the scope of the measurement and study population.

The record marks the study as terminated and reports enrollment of 13. It does not give the reason for termination or explain whether the study reached its intended completion. The original statistical plan, sample-size justification, missing-data methods, and sponsor analyses are not reported in the registry record. These gaps, together with the limited precision of the posted comparisons, constrain what can be concluded.

The safety summaries report no serious adverse events or deaths in the listed conditions, alongside non-serious event counts. These descriptive counts do not establish comparative safety, particularly without details on event types, exposure, timing, or analysis. Overall, the posted record is informative about the outcome definitions and the observed summaries, but it does not settle the broader clinical question.

17. Why This Trial Matters Statistically

This study raises several statistical issues that are especially important for clinical researchers. First, it uses a crossover design, while the posted comparisons are simple unadjusted recalculations from arm summaries. Crossover designs can use within-participant comparisons, and the relationship between measurements from the same participant can affect precision. Without the participant-level data or a reported crossover analysis, the recalculated contrasts cannot show how the intended design was analyzed.

Second, the primary outcome is an indirect physiological measure derived from skin temperature after a cold challenge. The measurement protocol and aggregation across eight fingers are described, but the record does not report a threshold for a meaningful difference. Statistical evidence about a measured outcome and clinical interpretation of that outcome are related but not interchangeable.

Third, the primary estimates are uncertain. Their confidence intervals span zero and cover a broad range of possible mean differences. The point estimates alone should not be used to tell a confident story about direction or magnitude. A limited amount of information and outcome variability can leave estimates imprecise, while the missing crossover-specific details prevent a complete assessment of the uncertainty calculation.

Finally, the record lists multiple secondary outcomes but does not report a multiplicity strategy or secondary analyses. This makes it important to treat secondary comparisons as exploratory rather than as independent confirmation. The sample-size illustrations can help readers understand how target effects and power relate under stated assumptions, but they do not establish the study's original planning or its achieved power. Together, these features show why design-aware analysis, prespecification, and transparent reporting matter when interpreting trial results.

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.

Several limitations are specific to the information reported for this trial. Although the study is identified as crossover, the record does not describe the treatment sequence, periods, washout arrangements, or timing of measurements under each condition. It also does not report whether the comparisons account for treatment period, sequence, or within-participant correlation. Consequently, the unadjusted recalculations from arm-level summaries may not reflect the analysis that would use the crossover structure.

The record lists enrollment of 13 and marks the study as terminated. It does not report why the study was terminated, whether termination affected the planned data collection, or whether all randomized participants contributed complete measurements. The original sample-size justification and assumptions are also not reported, so the observed enrollment cannot be compared with a documented target.

The primary outcome is an indirect assessment of digital blood flow based on skin temperature. The registry describes the cold challenge, infrared thermography, observation period, and finger averaging, but does not provide a clinically meaningful threshold. The relationship between this physiological measure and participants' symptoms or functioning is not established in the record.

For the posted results, the registry does not report participant-level data, distributions, missing-data methods, sensitivity analyses, or a sponsor analysis of the primary comparison. It does not report a multiplicity plan for the many secondary outcomes. These limitations restrict assessment of both the robustness of the estimates and the weight that should be placed on exploratory comparisons. The summary results should therefore be interpreted as limited descriptive evidence, not as a complete account of the planned trial analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study to Assess the Effect of Oral Temanogrel on Digital Blood Flow in Adult Participants With Raynaud's Phenomenon Secondary to Systemic Sclerosis — NCT04915950.
• Registry record last updated 2023-12-22; status last verified 2023-12.
• Results first posted 2023-12-22.
• 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

NCT04915950 is a Phase 2, multicenter, randomized, double-blind, placebo-controlled crossover study of oral temanogrel in adults with Raynaud's phenomenon secondary to systemic sclerosis. The registry lists enrollment of 13, a start date of 2021-11-03, a primary completion date of 2022-09-02, and status as terminated.

The primary outcome was rewarming area under the curve during 30 minutes after a cold challenge, assessed indirectly using infrared thermography. Posted arm means were 43,910 for temanogrel 120 mg, 44,000 for temanogrel 60 mg, and 44,530 for placebo. Unadjusted recalculated comparisons had broad confidence intervals spanning zero. The registry record does not report a sponsor analysis, the reason for termination, or the original statistical plan.