‘B. Quintiles [i.e. IQVIA UK] and Sponsor [i.e. Cardiorentis] are the parties to a General Services Agreement dated29 May 2012 and made between Sponsor and Quintiles (“First GSA”); this follows an Authorization to Proceed Agreement dated26 August 2011 and made between Euronyme GmbH (“Euronyme”) and Quintiles and the subsequent novation of Euronyme’s rights and obligations to Sponsor under the Novation and Amendment Agreement made between the parties hereto and Euronyme on7 November 2011 . The said Authorization to Proceed Agreement as novated and amended is referred to below as “the ATP”.’
‘Services to be Provided. The services to be performed hereunder (the “Services”) shall be specified in the Scope of Work attached hereto as Attachment 1 (including some services already carried out under the ATP and First GSA). Any regulatory obligations or other responsibilities not specifically transferred in this Agreement shall remain the responsibility of Sponsor.’
‘Quintiles will be responsible for planning and coordinating 4 2-day investigator meeting(s) for up to 194 sites with up to 452 attendees, including sites (388), Sponsor (15), and Quintiles (49) attendees participating. In collaboration with meeting planners to be contracted ad hoc for the events.’ (2). Clinical Operations Detail: Site Initiation Visits ‘Quintiles will perform 194 site initiation visits based on 194 total sites’. (3). Clinical Operations Detail: Interim Monitoring Visits ‘Quintiles will conduct appropriate number of interim monitoring visits based on 204,926 total CRF [Case Report Form] pages with an average review time of 4 minutes per CRF page. 100% SDV [viz Source Data Verification, explained below] is assumed for budget purposes, however an SDV planned (sic) for reduced SDV will be issued during the study, in order to use the additional time to SDV Endpoint and SAE data’ (4). Medical Monitoring Detail: Medical Monitoring ‘Quintiles’
‘If Quintiles shall fail to meet one or more of the targets then Quintiles will not earn back the applicable proportion of the discount …’
‘Change Orders. Any change in the details of this Agreement or the assumptions upon which this Agreement is based … may require changes in the budget and/or time lines, and shall require a written amendment to the Agreement (a “Change Order”)…’
‘7.0 a) Ownership and Inventions. Excluding Quintiles’
‘16.0 Limitation of Liability. (a) Neither Quintiles, nor its affiliates, nor any of their respective directors, officers, employees, subcontractors or agents shall have any liability (including without limitation, contract, negligence and tort liability) for any loss of profits, opportunities or goodwill or any type of indirect or consequential damages in connection with this Agreement or the Services performed by Quintiles. (b) In no event shall the collective, aggregate liability (including without limitation, contract, negligence and tort liability) of Quintiles or its affiliates, directors, officers, employees, subcontractors or agents under this Agreement exceed the amount of fees actually received by Quintiles from Sponsor under this Agreement. …’
‘Improvement in a hierarchical clinical composite comprised of elements associated with: patient global assessment using a 7-point scale of symptomatic improvement, lack of improvement, or worsening; persistent or worsening heart failure (HF) requiring an intervention (initiation or intensification of IV therapy, circulatory or ventilatory mechanical support, surgical intervention, ultrafiltration, hemofiltration or dialysis); and all-cause mortality. Assessment of the clinical composite will be performed at 6 hour (h), 24 h and 48 h after start of IV ularitide infusion. Patients will be classified as “improved” if the patients are moderately or markedly improved at all 3 time points (at 6h, 24 h and 48 h) and do not fulfil criteria for “worse” during the first 48 hours following the start of the study drug infusion. Patients will be classified as “worse” if (during the 48 h) they die; experience worsening HF requiring a prespecified intervention at any time during the first 48 h; or experienced moderate or marked worsening of their global assessment at any of the 3 time points (at 6 h, 24 h or 48 h).’
‘The number of subjects in a clinical trial should always be large enough to provide a reliable answer to the questions addressed. This number is usually determined by the primary objective of the trial. If the sample size is determined on some other basis, then this should be made clear and justified. For example, a trial sized on the basis of safety questions or requirements... may need larger numbers of subjects than a trial sized on the basis of the primary efficacy question... The method by which the sample size is calculated should be given in the protocol, together with the estimates of any quantities used in the calculations... In confirmatory trials, assumptions should normally be based on published data or on the results of earlier trials. The treatment difference to be detected may be based on a judgement concerning the minimal effect which has clinical relevance in the management of patients or on a judgement concerning the anticipated effect of the new treatment, where this is larger...’
‘Based on previous studies of ularitide, 46.9% of the patients receiving ularitide 15 ng/kg/min and 22.4% of the patients receiving placebo were successful in achieving marked or moderate improvement of dyspnea at 6 h which was still apparent at 24 h. In the proposed Phase III trial, the evaluation of the composite endpoint will compare the distributions of patients who have improved, are unchanged, or who have worsened. It will be assumed that this distribution in the placebo group will be 25% improved, 50% unchanged, and 25% worsened. It is expected that use of ularitide will result in a relative increase of 50% in the percentage of patients who have improved, and a relative decrease of 33% in the percentage of patients who have worsened. As a result, the expected distribution of responses in the ularitide group is 37.5% improved, 45.8% unchanged, and 16.7% worsened.’
‘The primary safety endpoint will evaluate the non-inferiority of ularitide to placebo in the rate of death or first rehospitalization for cardiovascular reasons at Day 30. Based on prior published data, the 30-day safety event rate in the placebo group is estimated to be 16%. The safety event rate of 14.9% is assumed in the ularitide group (corresponding to observed risk ratio of 0.93 from ASCEND-HF trial). Demonstrating the non-inferiority of the ularitide safety event rate to placebo within a non-inferiority margin of 4% using an exact binomial test (overall Type I error = 0.025, 1-sided; 90% power; 1:1 randomization) will require 1,058 evaluable patients per treatment group.’
‘1) Males and females aged 18 to 85 years 2) Unplanned hospitalization or emergency department visit for ADHF. Acute HF is defined as including all of the following: a) Dyspnea at rest in a recumbent position (30 to 45 degrees), which has worsened within the past week. b) Radiological evidence of HF on a chest X-ray. c) BNP >500 pg/mL or NT-pro BNP >2000 pg/mL 3) Ability to start infusion of the study drug within 12h after initial clinical assessment performed by a physician at the emergency room/hospital with symptoms of ADHF.’
‘6) Persisting dyspnea at rest despite standard background therapy for ADHF (as determined by the Investigator) which must include IV furosemide (or equivalent diuretic) at ≥40 mg (or its equivalent) at any time after start of emergency services (ambulance, emergency department, or hospital). At the time of randomization, the patient must still be symptomatic. In addition, the patient should not have received an IV bolus of a diuretic for at least 2 h prior to randomization, and the infusion rates of all ongoing IV infusions must not have been increased or decreased for at least 2 h prior to randomization.’
‘3) Treatment with levosimendan, milrinone, or any other phosphodiesterase inhibitor within 7 days before randomization.’
‘The Full Analysis set (also ITT [ie Intention to Treat]) will be the primary analysis population. The primary efficacy analysis will be carried out on the 2-sided 0.99% level. The primary safety analysis will be carried out on the 1-sided 2.45% level. Nominal p-values will be presented for additional supportive analysis. Statistical tests on the primary efficacy endpoint will be repeated on the Per Protocol (PP) population to check the robustness of the test results.’
‘There will be 3 analysis populations defined for this study: •. The Full analysis set (FAS; ITT) will be defined as all randomized patients, according to the ITT principle. •. The PP analysis set will be defined as patients in the FAS who do not have any major protocol deviations during the study treatment. Protocol deviations will be identified and documented following a blind data review prior to database lock. •. The As Treated (AT) set will be defined as all patients who received the study drug (active or placebo) classified according to the treatment that they actually received.’
‘Details of imputations for missing data will be presented in the Statistical Analysis Plan (SAP), which will be finalized prior to database lock and study unblinding.’
‘If your proposed primary efficacy endpoint has favorable effects on global clinical assessment only and no adverse effects on mortality, a single trial with a highly significant p-value, as you are currently planning, would be required for approval of ularitide. Lacking this, a second trial would be required. Also, if the effect is all on the global assessment, you may not have an adequately reassuring safety database.’
‘Results from Novartis Phase III study show that RLX030 [seralaxin] reduced deaths in patients with acute heart failure’
‘Phase III study results show that investigational RLX030 (seralaxin) reduced all-cause mortality in patients with acute heart failure (AHF). The six-month RELAX-AHF study shows that RLX030 reduces the number of deaths in patients with this disease, which has a higher mortality rate than most other cardiovascular diseases.’
‘- The original clinical composite primary endpoint (consisting of use of 7-point patient global assessment of symptomatic improvement, assessment of patient improvement/worsening, and death) would continue to be evaluated for superiority to placebo with an assigned alpha of 0.01. - A new cardiovascular mortality (using a time-to-event analysis) would be evaluated for superiority to placebo with an alpha of 0.04. To evaluate this endpoint, the trial would continue until a total of 655 cardiovascular deaths had occurred.’
‘Primary Efficacy Analyses The following hypotheses will be tested: Co-primary efficacy endpoint 1 H 0: There is no difference in the distribution of hierarchical composite variable in the 2 treatment groups i.e., ularitide and placebo The alternative hypothesis will be 2-sided and is stated as: H 1: There is a difference in the distribution of hierarchical composite variable in the 2 treatment groups. The primary efficacy analysis for co-primary endpoint 1 will be performed on the FAS. The composite primary efficacy endpoint will be tested using the Cochran-Mantel-Haenszel test for singly ordered data (with time from first physician evaluation to the start of study drug infusion [≤6h vs >6h] and baseline SBP [≤ median vs.>median] as stratification variables) to compare results between treatment groups. A final p-value of 0.01 or less (2-sided) will be considered evidence of statistically significant superiority. Co-primary efficacy endpoint 2 H 0: There is no difference in the cardiovascular mortality between the 2 treatment groups The alternative hypothesis will be 2-sided and is stated as: H 1: There is a difference in the cardiovascular mortality between the 2 treatment groups. The primary efficacy analysis for co-primary efficacy endpoint 2 will be a time-to-event analysis performed on the FAS. The endpoint will be tested using a Cox proportional hazards regression analysis to compare results between treatment groups, with age, gender, SBP at baseline, the time (in hours) from the first physician evaluation to start of study drug infusion (≤6 h vs. >6 h), and region (North America, Latin America, Europe) included as covariates. A final p-value < 0.04 (2-sided) for the coefficient associated with study group — adjusted for interim analyses according to a Lan-DeMets spending function, as described in the DSMB charter and the SAP — for treatment group will be considered evidence of statistically significant superiority.’
‘Co-primary efficacy endpoint 2: cardiovascular mortality Cardiovascular mortality will be evaluated in a time-to-event Cox proportional hazards regression analysis. It is assumed that the risk of cardiovascular mortality will be 11.0% per 6-month period of follow-up in the placebo group and that this risk will be reduced by a relative 22% in the ularitide group to a rate of 8.58% per 6 months. Based on these assumptions, an overall Type I error level = 0.04 (2-sided), 90% power, and a Kaplan-Meier log-rank analysis to estimate sample size, a total of 682 cardiovascular deaths would be required to demonstrate superiority of ularitide. If enrollment takes place over a 2-year period and there is a minimum follow-up of 1 year, a total enrollment of 2,152 subjects is estimated to be required.’
‘...under the direction of the DSMB, an analysis will be carried out to estimate conditional power when 50% of the number of cardiovascular deaths needed for evaluation of primary efficacy endpoint 2 (approximately 341 deaths) has been documented, or alternatively, when enrollment is expected to be completed within 60 days, whichever occurs first. The interim analysis will be based on only data collected for co-primary efficacy endpoint 2 and will be used to estimate the conditional power to achieve the original primary study objective and to potentially adaptively re-estimate the sample size requirement for this endpoint. The specific details regarding the DSMB organization and procedures will be outlined in the DSMB Charter and a separate SAP will be produced covering the analysis required.’
‘Project Quality Issues at IQVIA's monitored sites / facilities or processes associated with the TRUE-AHF trial would be processed by IQVIA's staff assigned to the TRUE-AHF trial in accordance with SOP CS_OP_QA002: Managing Quality Issues including suspected misconduct. Confirmed quality issues were to be escalated to the IQVIA Global QA Lead, who would escalate confirmed critical quality issues to the assigned Cardiorentis QA representative according to SOP CS_OP_QA002.’
‘Confirmed Critical Quality Issues will be notified to Cardiorentis QA within one business day of being confirmed as critical by IQVIA QA and major quality issues would be notified to Cardiorentis within seven business days of IQVIA being notified. Both IQVIA QA and Cardiorentis would work together to resolve quality issues, determine the root cause and generate an effective CAPA [Corrective and Preventive Action] plan.’
‘Site training Sites will be trained on the protocol procedures by the CRA during the Site Initiation Visit (SIV) and if necessary during subsequent Monitoring visits. The Quintiles CRA is responsible for ensuring that all site training is documented by the site personal (sic) in the site specific Training Log.’
‘CRA will be completing review of all source documents against data entered into the eCRF.’
‘Protocol deviations that occurred at the sites will be identified during Monitoring visits, in-house review and other site contacts. The CRA is responsible for discussing identified issues with the PI and the relevant site staff in a timely manner and to follow up on actions related to protocol deviations until resolution… If possible, for each deviation the actual root cause that caused the event should be identified, by discussing with the site the actual reason for the PD occurrence. … Preventive actions to avoid the deviations happening again are also expected to be discussed and agreed with the PI. The CRA identifying the deviation has to track all detected deviations in CTMS within 10 days of the identification and has to update CTMS entries with new information obtained as well as the closure date. If there are critical PDs identified or site non-compliance suspected, the responsible CPM must be informed immediately via email or phone within 24 hours of identification.’
‘The primary efficacy analysis for co-primary efficacy endpoint 1 will be carried out with a 2-sided 1% significance level. The final analysis for co-primary efficacy endpoint 2 will be carried out with a 2-sided 4% significance level. For all other analysis the default significant level will be (5%); confidence intervals will be 95% and all tests will be two-sided.’
‘The eCRF and the protocol are both confidential. The eCRF will be created by the CRO and programmed into the electronic data capture (eDC) system. All study centers will need internet access to access the eCRFs and will only have access to data for patients at their own study centers. Data management (DM) and other coordinator teams will have access to data at all study centers. All eCRFs are to be completed by an authorized member of the investigational staff and reviewed and signed by the Investigator. All entries, corrections, and alterations are to be made by the responsible Investigator or an authorized member of the investigational staff. All eCRFs are to be completed in a manner that ensures accurate interpretation of data within 72 h of each study visit. It is each Investigator's responsibility to ensure that all discontinued orders or changes in the study or other medications entered on the patient's eCRF correspond to the entries on the patient's medical records. The eCRFs for any patient leaving the study should be completed at the time medication is terminated for whatever reason. The eCRFs must accurately reflect data contained in patient's records (e.g., source documents). After data is entered into the eCRF by the site, queries that are generated by the eDC system should be addressed by the site. Data queries will be raised for inconsistent, impossible, or missing data. All entries to the study database will be available in an audit trail. Data Management or other parties involved can also raise manual queries for sites to address (e.g., for coding queries). The same process is to be followed by any other groups creating manual queries in the eDC system (e.g., for SAE reconciliation). Once all data is entered, source document verification (SDV) completed on required fields, manual queries and electronic data reconciliation completed and all queries closed, the casebook can be signed by the Principal Investigator. Once the casebook is signed, DM will then lock the casebook so that no modifications can be made.’
‘These worksheets will be used to document important data points collected during the study. In some cases required information might be documented in other locations, for example, the subject medical record and do not need to be copied into these worksheets if they are known to be available elsewhere. It is important to collect all necessary data at the time-point specified in the protocol and flowchart. All source documentation needed to determine eligibility for enrolment and for collection of data after start of study drug infusion should be completed in “Real Time”; do not complete them retrospectively.’
‘A query must be answered within 3 working days of receipt. 3 weeks prior to database lock this timeline is reduced to 24h. During the maintenance phase of the study please check the eCRFs at least twice a week for any newly issued queries to meet the timeline. Your CRA will review query resolution on an ongoing basis and will contact you should your site continually not respond to queries within 3 days of receipt. Metrics for query turnaround times are closely monitored.’
‘As part of its oversight activities, [Cardiorentis] conducts remote data review of pre-selected investigational sites and patients randomized in TRUE-AHF. … As stated in the [Cardiorentis] oversight plan for [the study], the target is to review about 20% of all patients enrolled. … Process: The patient data review by the Sponsor is carried out on data available remotely in read only access. … Quality Assessment of Individual Patient Data Review in eCRF … The data review … is focused on consistency in completeness of all required data entries, within eCRF, trends in potentially missed endpoints, adverse events and/or protocol deviations…. In addition, planned treatment, concomitant medication and medication list at hospital discharge / day30 are checked for completeness and consistency. Within the review of ConMed section, any signs of increased AHF therapy and forbidden medication are closely reviewed. …’
‘The checking and assessment of data during the period of time between trial completion (the last observation on the last subject) and the breaking of the blind, for the purpose of finalising the planned analysis.’ (b). Section 5.1 of ICH-GCP E9, headed, ‘Prespecification of the Analysis’, states, inter alia, as follows: ‘When designing a clinical trial the principal features of the eventual statistical analysis of the data should be described in the statistical section of the protocol. This section should include all the principal features of the proposed confirmatory analysis of the primary variable(s) and the way in which anticipated analysis problems will be handled. In case of exploratory trials this section could describe more general principles and directions. The statistical analysis plan … may be written as a separate document to be completed after finalising the protocol. In this document, a more technical and detailed elaboration of the principal features stated in the protocol may be included …. The plan may include detailed procedures for executing the statistical analysis of the primary and secondary variables of the data. The plan should be reviewed and possibly updated as a result of the blind review of the data … and should be finalised before breaking the blind. Formal records should be kept of when the statistical analysis plan was finalised as well as when the blind was subsequently broken… If the blind review suggests changes to the principal features stated in the protocol, these should be documented in a protocol amendment. Otherwise, it will suffice to update the statistical analysis plan with the considerations suggested from the blind review. Only results from analyses envisaged in the protocol (including amendments) can be regarded as confirmatory. In the statistical section of the clinical study report the statistical methodology should be clearly described including when in the clinical trial process methodology decisions were made (see ICH E3).” (c). Section 5.2 of ICH-GCP E9 gives guidance on the consideration of analysis sets and states inter alia as follows: ‘The set of subjects whose data are to be included in the main analyses should be defined in the statistical section of the protocol. In addition, documentation for all subjects for whom trial procedures (e.g. run-in period) were initiated may be useful. The content of this subject documentation depends on detailed features of the particular trial, but at least demographic and baseline data on disease status should be collected wherever possible. If all subjects randomised into a clinical trial satisfied all entry criteria, followed all trial procedures perfectly with no losses to follow-up, and provided complete data records, then the set of subjects to be included in the analysis would be self-evident. The design and conduct of a trial should aim to approach this ideal as closely as possible, but, in practice, it is doubtful if it can ever be fully achieved. Hence, the statistical section of the protocol should address anticipated problems prospectively in terms of how these affect the subjects and data to be analysed. The protocol should also specify procedures aimed at minimising any anticipated irregularities in study conduct that might impair a satisfactory analysis, including various types of protocol violations, withdrawals and missing values. The protocol should consider ways both to reduce the frequency of such problems, and also to handle the problems that do occur in the analysis of data. Possible amendments to the way in which the analysis will deal with protocol violations should be identified during the blind review. It is desirable to identify any important protocol violation with respect to the time when it occurred, its cause and influence on the trial result. The frequency and type of protocol violations, missing values, and other problems should be documented in the clinical study report and their potential influence on the trial results should be described (see ICH E3). Decisions concerning the analysis set should be guided by the following principles: 1) to minimise bias, and 2) to avoid inflation of type I error.’ (d). Section 5.2.1 of ICH-GCP E9 headed ‘Full Analysis Set’ states inter alia as follows: “The intention-to-treat … principle implies that the primary analysis should include all randomised subjects. Compliance with this principle would necessitate complete follow-up of all randomised subjects for study outcomes. In practice this ideal may be difficult to achieve, for reasons to be described. In this document the term ‘full analysis set’ is used to describe the analysis set which is as complete as possible and as close as possible to the intention-to-treat ideal of including all randomised subjects. Preservation of the initial randomisation in analysis is important in preventing bias and in providing a secure foundation for statistical tests. In many clinical trials the use of the full analysis set provides a conservative strategy. Under many circumstances it may also provide estimates of treatment effects which are more likely to mirror those observed in subsequent practice.” (e). Section 5.2.2 of ICH-GCP E9 headed ‘Per Protocol Set’ states inter alia as follows: ‘The ‘per protocol’ set of subjects, sometimes described as the ‘valid cases’, the ‘efficacy’ sample or the ‘evaluable subjects’ sample, defines a subset of the subjects in the full analysis set who are more compliant with the protocol and is characterised by criteria such as the following: i) the completion of a certain pre-specified minimal exposure to the treatment regimen; ii) the availability of measurements of the primary variable(s); iii) the absence of any major protocol violations including the violation of entry criteria. The precise reasons for excluding subjects from the per protocol set should be fully defined and documented before breaking the blind in a manner appropriate to the circumstances of the specific trial. The use of the per protocol set may maximise the opportunity for a new treatment to show additional efficacy in the analysis, and most closely reflects the scientific model underlying the protocol. However, the corresponding test of the hypothesis and estimate of the treatment effect may or may not be conservative depending on the trial; the bias, which may be severe, arises from the fact that adherence to the study protocol may be related to treatment and outcome. The problems that lead to the exclusion of subjects to create the per protocol set, and other protocol violations, should be fully identified and summarised. Relevant protocol violations may include errors in treatment assignment, the use of excluded medication, poor compliance, loss to follow-up and missing data. It is good practice to assess the pattern of such problems among the treatment groups with respect to frequency and time to occurrence.’ (f). Section 5.2.3 of ICH-GCP E9 headed ‘Roles of the Different Analysis Sets’ states inter aliaas follows: ‘In general, it is advantageous to demonstrate a lack of sensitivity of the principal trial results to alternative choices of the set of subjects analysed. In confirmatory trials it is usually appropriate to plan to conduct both an analysis of the full analysis set and a per protocol analysis, so that any differences between them can be the subject of explicit discussion and interpretation. In some cases, it may be desirable to plan further exploration of the sensitivity of conclusions to the choice of the set of subjects analysed. When the full analysis set and the per protocol set lead to essentially the same conclusions, confidence in the trial results is increased, bearing in mind, however, that the need to exclude a substantial proportion of subjects from the per protocol analysis throws some doubt on the overall validity of the trial. The full analysis set and the per protocol set play different roles in superiority trials (which seek to show the investigational product to be superior), and in equivalence or non-inferiority trials (which seek to show the investigational product to be comparable, see section 3.3.2). In superiority trials the full analysis set is used in the primary analysis (apart from exceptional circumstances) because it tends to avoid over-optimistic estimates of efficacy resulting from a per protocol analysis, since the non-compliers included in the full analysis set will generally diminish the estimated treatment effect. However, in an equivalence or non-inferiority trial use of the full analysis set is generally not conservative and its role should be considered very carefully.’
‘The per-protocol (PP) analysis set will contain all patients in the FAS who did not experience any major protocol deviations during the study treatment. Major protocol deviations will be identified and documented following a blind data review following database lock. Protocol violations to be examined at the blind data review include: •. Failure of any inclusion/exclusion criteria •. Did not complete the 48 hours of study treatment •. >12 h between initial clinical assessment and start of study drug infusion •. Received a concomitant medication during study treatment which may affect the efficacy of study treatment •. Received study treatment other than the one to which they were randomized Full details of the definition of major protocol violations will be included in the Blind Data Review (BDR) plan.’
‘As you know, SAP Section 5.3 says that the per-protocol (PP) analysis set will contain all patients in the FAS who did not experience any major protocol deviations during the study treatment. The SAP language was intentionally made general. The goal of the PP analysis, is to get a "clean" estimate of the treatment effect, without confounding factors. We have some flexibility in defining the PP population as long as it is done in a blinded manner and not favouring one treatment arm. And these are the violations the SAP says are to be included in the blind data review: • Failure of any inclusion/exclusion criteria • Did not complete the 48 hours of study treatment • >12 h between initial clinical assessment and start of study drug infusion • Received a concomitant medication during study treatment which may affect the efficacy of study treatment • Received study treatment other than the one to which they were randomized I suggest we need to start thinking about any other, if any, criteria should be included.’
‘However, the PD log is inconsistent in the description of deviations and the level of detail given. Plus, there is no guarantee, that all PDs are captured. This means we may have to do a for purpose data extraction.’
‘Objective A: Defining and identifying major protocol violations/deviations (PV/PDs) for the purpose of establishing the analysis populations prior to database un-blinding. Objective B: Identifying any unresolved data issues (accuracy, consistency, outlying, missing, un-coded) in the run up to database lock. Objective C: Discuss any data issues which may affect the efficacy analysis or may require revision of the Statistical Analysis Plan (SAP) prior to database un-blinding.’
‘Major PDs excluding patients from the Per Protocol population will be documented in the PD Spreadsheet. The rationale for the criteria are described in Section 7.2.1. The PD Spreadsheet will be a combined version of the CTMS PD log spreadsheet and a BIOS programmed PD spreadsheet, as the two sources of identifying PDs for PP exclusions (see Table 1). For potential major PDs requiring review a column will be included in the spreadsheet to document the final BDR team decision. In general, the ULA01 BDR team approach to the PP population will be to exclude patients only if proven ineligible, either by CRA source data verification and reporting in CTMS or by data entry in eCRF, rather than to include patients only if proven eligible. For example, lack of eCRF evidence to support an eligibility criterion (such as missing eCRF CONMED page IV diuretic entries to support inclusion criterion 6) may be a PD for data entry. However, this may not be proof that the required amount of IV diuretic was not administered at least two hours before randomization. Unless specifically stated in the CTMS PD log that this component of inclusion criterion 6 was not met, missing appropriate IV diuretic records in CONMED may not result in a confirm PDV02 failed eligibility finding and the patient may still be included in the PP population.’
‘While the data may be reliable, SCI has concerns about Quintiles's conduct of the TRUE-AHF trial on the basis the proportion of subjects randomized in violation of eligibility criteria, and the drastically different results among the eligible and ineligible populations. According to Quintiles's original sensitivity analysis of observed data only, there was no significant difference between the subjects randomized to ularitide and the subjects randomized to placebo with regard to co-primary efficacy endpoint 1, which indicates short-term clinical outcome (nominal p = 0.33). When SCI removed all ineligible subjects from its analysis of co-primary efficacy endpoint 1, subjects randomized to ularitide had significantly better outcomes compared to subjects randomized to placebo (nominal p = 0.035). When SCI limited analysis of co-primary efficacy endpoint l to the ineligible population, subjects randomized to ularitide had significantly worse short-term clinical outcomes compared to subjects randomized to placebo (nominal p = 0.022). The radical differences between the results in the eligible and ineligible population raise concerns not only about the potential missed efficacy signal in the ITT analysis of the TRUE-AHF study, but more importantly, about potential undue harm to the ineligible patients who were randomized.’
‘In November 2016, Cardiorentis notified SCI that Quintiles had randomized 358 subjects who did not meet the protocol's eligibility criteria. Cardiorentis provided SCI a list of the subjects and the criteria that had been violated. The largest number of ineligibles were violators of exclusion criterion 3: "treatment with levosimendan, milrinone, or any other phosphodiesterase inhibitor within 7 days before randomization" and inclusion criterion 6: Persisting dyspnea at rest despite standard background therapy for ADHF (as determined by the Investigator) which must include IV furosemide (or equivalent diuretic) at >_40 mg (or its equivalent) at any time after start of emergency services (ambulance, emergency department, or hospital). At the time of randomization, the patient must still be symptomatic. In addition, the patient should not have received an IV bolus of a diuretic for at least 2 h prior to randomization and the infusion rates of ongoing IV infusions must not have been increased or decreased for at least 2 hours prior to randomization. Cardiorentis asked SCI to evaluate co-primary endpoint 1 in the following ways: • removing subjects who violated exclusion criterion 3; and • removing subjects who violated inclusion criterion 6; and • removing subjects who violated exclusion criterion 3 or inclusion criterion 6; and, • removing all ineligible subjects. In addition, SCI analyzed co-primary endpoint 1 in the subset of ineligible subjects. Enrollment of ineligible subjects had a noticeable impact on the results of co-primary endpoint 1 …. For example, when the analysis included all ineligibles, 47.5% of placebo subjects and 48.6% of ularitide subjects improved (nominal p-value comparing distributions = 0.33). Excluding all ineligibles decreases the proportion of placebo subjects improving to 45.8% and increases the proportion of ularitide subjects to 49.8% (nominal p- value = 0.035). Limiting the analysis to ineligible subjects shows that the difference between the groups is significant (nominal p-value = 0.022), and in favor of placebo (56.4% of placebo and 42.7% of ularitide subjects improved).’
‘As a result of SCI’s investigation, we believe that the study produced a reliable dataset from which valid conclusions may be drawn about the co-primary endpoints. Given the findings in Section 3.1.5, SCI was not confident in the accuracy of the chemistry data; however, after review of additional selected laboratory parameters, SCI did not detect any meaningful differences based on its analyses of the eCRF CHEM and HEMA data compared to the results that Quintiles reported in the HER. While the data may be reliable, SCI has concerns about the proportion of subjects randomized in violation of eligibility criteria, and the fact that the eligible and ineligible populations showed results on co-primary endpoint 1 that were numerically in opposite directions. Quintiles's original sensitivity analysis of observed data only showed no significant difference between the subjects randomized to ularitide and the subjects randomized to placebo with regard to co-primary endpoint 1 (nominal p-value = 0.33). When SCI removed all ineligible subjects from the analysis of co-primary endpoint 1, subjects randomized to ularitide had significantly better outcomes compared to subjects randomized to placebo (nominal p-value = 0.035). Analysis of co-primary endpoint 1 limited to the ineligible population showed that subjects randomized to ularitide had numerically worse outcomes on co-primary endpoint 1 compared to subjects randomized to placebo (nominal p-value = 0.022). These differences between the results in the eligible and ineligible population raise concerns about the interpretation of data from the ITT population.’
‘… it seems clear, from review of the original trial protocol (dated April 19, 2012) and the final protocol (dated December 8, 2014) that the “acute injury hypothesis” was not contemplated at the time of the original trial design, nor was the trial originally designed to test this hypothesis… Based on the comments in Amendment 1 about the acute injury hypothesis, it seems clear that this concept of the trial was adopted at the same time as the addition of a new co-primary end point to the trial – that being cardiovascular mortality. … The revised manuscript should begin with a clear indication that the original trial hypothesis was based on the demonstration of short-term symptomatic efficacy with intermediate-term safety. It should then indicate that the demonstration of a possible long-term effect on mortality in RELAX-AHF led to the revision of the TRUE-AHF hypothesis to encompass the test of the “acute injury” concept, including the potential for a reduction in acute injury to lead to a long-term survival benefit.’
‘The revised version of the manuscript now makes clear the trial’s original hypothesis (i.e. evaluation of the short-term effects of ularitide) and the conversion of the trial shortly after its onset to a cardiovascular mortality trial, with the specific intent of testing the “acute distension-myocardial injury” hypothesis.’ (2). The Editors asked why, under the original hypothesis, ularitide had been chosen. Specific questions included: if a vasodilator was thought likely to be effective, why not test IV nitroglycerin? Was a diuretic effect anticipated, and if so why as no such effect had previously been documented in major trials of natriuretic peptides? Why choose this drug to achieve symptom relief, and, generally, ‘why should ularitide be superior to standard therapy (aggressive use of IV diuretics, perhaps most importantly) in this setting?’
‘We did not anticipate nor have we claimed that ularitide has unique properties. Ularitide does differ from other natriuretic peptides (e.g. its endogenous source is the kidney rather than the heart, and its degradation is resistant to neprilysin). However, the selection of ularitide was not based on the uniqueness of its chemistry or physiology, but on the uniqueness of having a Sponsor with the willingness and resources to launch a large-scale trial to evaluate the drug’s efficacy. The investigators grasped the availability of this funding source as a wonderful opportunity to test an important hypothesis about acute heart failure…’ (3). The Editors commented that they believed ‘that a trial originally focused on the acute injury hypothesis would, or at least probably would, be designed differently from TRUE-AHF….’
‘Although we can understand why the editors might think that a trial originally focused on the acute injury hypothesis might be designed differently from TRUE-AHF, this is truly not the case. Our original intent (even when the trial was focused only on short-term outcomes) was to administer the study drug as early as possible, based on our belief that time was of the essence even if the endpoints were entirely short-term…’ (4). One Reviewer had commented that the conclusion in the draft paper then under consideration was misleading as it did not address the fact that two co-primary endpoints were not met. Dr Packer answered: ‘The paper has been revised to make clear that neither of the two co-primary endpoints were met.’
‘BACKGROUND In patients with acute heart failure, early intervention with an intravenous vasodilator has been proposed as a therapeutic goal to reduce cardiac-wall stress and, potentially, myocardial injury, thereby favorably affecting patients’ long-term prognosis. METHODS In this double-blind trial, we randomly assigned 2157 patients with acute heart failure to receive a continuous intravenous infusion of either ularitide at a dose of 15 ng per kilogram of body weight per minute or matching placebo for 48 hours, in addition to accepted therapy. Treatment was initiated a median of 6 hours after the initial clinical evaluation. The coprimary outcomes were death from cardiovascular causes during a median follow-up of 15 months and a hierarchical composite end point that evaluated the initial 48-hour clinical course. RESULTS Death from cardiovascular causes occurred in 236 patients in the ularitide group and 225 patients in the placebo group (21.7% vs. 21.0%; hazard ratio, 1.03; 96% confidence interval, 0.85 to 1.25; P = 0.75). In the intention-to-treat analysis, there was no significant between-group difference with respect to the hierarchical composite outcome. The ularitide group had greater reductions in systolic blood pressure and in levels of N-terminal pro–brain natriuretic peptide than the placebo group. However, changes in cardiac troponin T levels during the infusion did not differ between the two groups in the 55% of patients with paired data. CONCLUSIONS In patients with acute heart failure, ularitide exerted favorable physiological effects (without affecting cardiac troponin levels), but short-term treatment did not affect a clinical composite end point or reduce long-term cardiovascular mortality.’
‘The first author, who had unrestricted access to the data, prepared the drafts of the manuscript, which were then reviewed and edited by all the authors, independent of the Sponsor. The authors assume responsibility for the accuracy and completeness of the analyses; the last author attests to the fidelity of the trial to the protocol.’
‘The coprimary outcome of death from cardiovascular causes occurred in 236 patients in the ularitide group and 225 patients in the placebo group (21.7% vs. 21.0%; hazard ratio, 1.03; 96% confidence interval [CI], 0.85 to 1.25; P = 0.75) (Table 2 and Fig. 2). The lack of a significant difference between the two groups was seen consistently across prespecified subgroups (except for a nominally significant interaction for geographical region), as well as in subgroups that were defined according to baseline levels of NT-proBNP and cardiac troponin (Fig. S3 in the Supplementary Appendix). The distribution of responses for the clinical composite (the second coprimary outcome) did not differ significantly between the groups (Table 2, and Table S3 in the Supplementary Appendix). In a post hoc analysis that excluded the patients who had been identified before the database lock as having been ineligible for the trial, a benefit of ularitide was shown with respect to the hierarchical clinical composite outcome (P = 0.03) but not with respect to cardiovascular mortality (Table S4 in the Supplementary Appendix). Because the tests for the two coprimary outcomes were not significant, and given the hierarchical testing plan, all secondary end-point analyses were exploratory. There was no benefit of ularitide for any of the clinical secondary outcome measures (Table 2).’
‘In the TRUE-AHF trial, ularitide exerted its expected short-term hemodynamic effects. The drug produced systemic vasodilation (as evidenced by decreases in systolic blood pressure), which was accompanied by decreases in NT-proBNP levels (reflecting a reduction in cardiac-wall stress). Both the hematocrit and serum creatinine levels increased during the infusion, pointing to hemo-concentration and (together with a decrease in liver enzymes indicative of less hepatic congestion) to aggressive decongestion; these effects were paralleled by a decrease in the rate of in-hospital heart-failure events during the infusion. Such early worsening events have been linked to increases in both cardiac filling pressures and cardiac troponin levels, which suggests that these events may reflect undertreated ventricular distention and acute cardiac injury at the time of initial admission. A reduction in cardiac-wall stress that is achieved rapidly after clinical presentation might be expected to reduce myocardial necrosis, preserve ventricular function, maintain clinical stability, and reduce the long-term risk of cardiovascular death. However, even though the time from clinical evaluation to pharmacologic intervention was shorter than in previous studies, and despite evidence of meaningful cardiac decongestion, the long-term risk of cardiovascular death was not reduced among patients who received ularitide. This lack of benefit raises doubt about the theories that early ventricular distention causes myocardial necrosis and adversely affect the natural history of heart failure after hospitalization and that rapid reversal of short-term ventricular distention preserves myocardial viability. For all the patients who underwent randomization, a clinical composite end point was also not affected by treatment.’
‘The justification for the use of this particular medication is not robust, since ularitide had been evaluated in only two previous studies involving a total of 245 patients who were treated for 24 hours. In addition, although a related natriuretic peptide, recombinant BNP (nesiritide), has been shown to have favorable short-term effects on hemodynamics and dyspnea relief, subsequent studies reported an increased risk of renal failure and a lack of survival benefit. Furthermore, hypotension was enough of a concern that patients who were enrolled in TRUE-AHF were required to have a minimum systolic blood pressure of 116 mm Hg, a criterion that unavoidably excluded the most compromised cohort of patients.’
‘In the final analysis of the TRUE-AHF trial, no differences in the coprimary end points were observed between ularitide and placebo. The overall proportion of patients in the placebo group who had short-term worsening of their condition was quite small, which suggests that the prospect of an ultimate success for ularitide was statistically limited. However, that is not to say that ularitide had a completely neutral effect; there were fewer in-hospital heart-failure events and greater reductions in NT-proBNP levels in the ularitide group than in the placebo group. Where does this leave us? We can conclude that ularitide, like its predecessor nesiritide, has limited short-term effects that wane after the discontinuation of treatment, which lessens the likelihood that there is a constructive avenue for further development of natriuretic peptides. It also appears that we do not have a mandate to establish rapid-response teams for patients who present with acute decompensated heart failure. At this point, we should remind ourselves that the primary immediate objective of treatment is the patient-centric goal of symptom relief. In addition, the idea that it is the hospitalization itself that increases the risk of cardiovascular death has been partially debunked, and not for the first time. This conclusion will allow us to change the focus from disease modification so that mortality is once again relegated to a safety, not an efficacy, end point. We also need greater consensus on how to define the response to an intervention and to determine which patients are in greatest therapeutic need (e.g., those with in-hospital worsening despite conventional therapy). In reality, there should be no surprise here. Exacerbations of chronic disease reflect the chronic disease, not the hospitalizations used to manage those exacerbations…’
‘We randomly assigned 7141 patients who were hospitalized with acute heart failure to receive either nesiritide or placebo for 4 to 168 hours in addition to standard care. Coprimary endpoints were the change in dyspnea at 6 and 24 hours, as measured on a 7-point Likert scale, and the composite end point of rehospitalization for heart failure or death within 30 days.’
‘Patients randomly assigned to nesiritide, as compared with those assigned to placebo, more frequently reported markedly or moderately improved dyspnea at 6 hours (44.5% vs. 42.1%, P = 0.03) and 24 hours (68.2% vs. 66.1%, P = 0.007), but the prespecified level for significance (P≤0.005 for both assessments or P≤0.0025 for either) was not met. The rate of rehospitalization for heart failure or death from any cause within 30 days was 9.4% in the nesiritide group versus 10.1% in the placebo group (absolute difference, −0.7 percentage points; 95% confidence interval [CI], −2.1 to 0.7; P = 0.31). There were no significant differences in rates of death from any cause at 30 days (3.6% with nesiritide vs. 4.0% with placebo; absolute difference, −0.4 percentage points; 95% CI, −1.3 to 0.5) or rates of worsening renal function, defined by more than a 25% decrease in the estimated glomerular filtration rate (31.4% vs. 29.5%; odds ratio, 1.09; 95% CI, 0.98 to 1.21; P = 0.11).’
‘Nesiritide was not associated with an increase or a decrease in the rate of death and rehospitalization and had a small, nonsignificant effect on dyspnea when used in combination with other therapies. It was not associated with a worsening of renal function, but it was associated with an increase in rates of hypotension. On the basis of these results, nesiritide cannot be recommended for routine use in the broad population of patients with acute heart failure.’
‘In this multicenter, double-blind, placebo-controlled, event-driven trial, we enrolled patients who were hospitalized for acute heart failure and had dyspnea, vascular congestion on chest radiography, increased plasma concentrations of natriuretic peptides, mild-to-moderate renal insufficiency, and a systolic blood pressure of at least 125 mm Hg, and we randomly assigned them within 16 hours after presentation to receive either a 48-hour intravenous infusion of serelaxin (30 μg per kilogram of body weight per day) or placebo, in addition to standard care. The two primary end points were death from cardiovascular causes at 180 days and worsening heart failure at 5 days.’
‘A total of 6545 patients were included in the intention-to-treat analysis. At day 180, death from cardiovascular causes had occurred in 285 of the 3274 patients (8.7%) in the serelaxin group and in 290 of the 3271 patients (8.9%) in the placebo group (hazard ratio, 0.98; 95% confidence interval [CI], 0.83 to 1.15; P = 0.77). At day 5, worsening heart failure had occurred in 227 patients (6.9%) in the serelaxin group and in 252 (7.7%) in the placebo group (hazard ratio, 0.89; 95% CI, 0.75 to 1.07; P = 0.19). There were no significant differences between the groups in the incidence of death from any cause at 180 days, the incidence of death from cardiovascular causes or rehospitalization for heart failure or renal failure at 180 days, or the length of the index hospital stay. The incidence of adverse events was similar in the two groups.’
‘In this trial involving patients who were hospitalized for acute heart failure, an infusion of serelaxin did not result in a lower incidence of death from cardiovascular causes at 180 days or worsening heart failure at 5 days than placebo.’
‘Among patients with AHF, a strategy of early intensive and sustained vasodilation, compared with usual care, did not significantly improve a composite outcome of all-cause mortality and AHF rehospitalization at 180 days.’
‘If the proportion of ineligible patients becomes unduly large, say 10% or more, this may reflect a generally poor standard of trial organisation which needs tightening up. On the other hand it can indicate that the trial’s eligibility criteria are too restrictive, so that investigators are finding that many patients they consider suitable are not actually eligible.’
‘3) Treatment with levosimendan, milrinone, or any other phosphodiesterase inhibitor within 7 days before randomization.’
‘Regarding the fact that this item has been highlighted as a finding for DM, I have checked how these deviations are usually tracked for other studies/Sponsors. For most of these studies, CRAs/Mas [medical advisors] are responsible for the identification of protocol deviations (including the use of prohibited medications). The identification of these deviations is based on SDV made by the CRA and the review of eCRFs/ patient profiles by the Mas without any involvement of DM. DM would specify and program protocol deviations checks if the identification of these deviations is included in DM SoW [scope of work] and managed within the eCRF (not CTMS). As we could have unreported deviations, I agree DM needs to be involved in the identification of this deviation by programming an automated check. However, this won’t replace a medical review and similar issues can exist regarding other type of protocol deviations.’
‘In accordance with our National Register of Drug, Aminophylline is classified in ksantin group of drug with primary bronchodilatative activity. Phosphodiesterase inhibition is dose dependent (Aminophylline dose, which is needed for PDE inhibition is significantly higher than Aminophylline dose for therapeutic bronchodilatative activity). … Please find below mail from our National coordinator, Professor Petar Seferovic: Dear All, We were recently (two weeks ago) notified that Aminophylline is listed as prohibited medication in the TRUE AHF study. In all versions of protocols, Levosimendan and Milrionone (sic), but not Aminophylline were highlighted by name as PDE3 inhibitors. According to Serbian pharmacological registry, Aminophylline is classified as brochodilatator (sic), and is widely used ONLY for that specific indication. The effects of the drug includes central (brain), bronchial and peripheral vascular effects, as well as mild diuretic properties. Per protocol, all drugs (including Aminophylline) can be used after randomization, as per physicians discretion. It came as a surprise that this issue arise after almost two years after the beginning of the study, probably because Aminophylline was not considered a specific PDE 3 inhibitor….’
‘6) Persisting dyspnea at rest despite standard background therapy for ADHF (as determined by the Investigator) which must include IV furosemide (or equivalent diuretic) at ≥40 mg (or its equivalent) at any time after start of emergency services (ambulance, emergency department, or hospital). At the time of randomization, the patient must still be symptomatic. In addition, the patient should not have received an IV bolus of a diuretic for at least 2 h prior to randomization, and the infusion rates of all ongoing IV infusions [of medication to treat HF] Words added in Protocol version 03. must not have been increased or decreased for at least 2 h prior to randomization.’
‘Once all eligibility criteria are met, and before randomization, the subject must still be symptomatic to be eligible for the study. In addition, HF-related IV medications must be unchanged over the last 2 hours. There is a risk the final evaluation prior randomization being missed.’
‘Inclusion criterion #6 (iv bolus and change of iv meds 2 hrs prior to random) misunderstood/neglected.’
‘Although the protocol states that any changes in on-going infusion within the 2 hours prior randomization would correspond to an exclusion criteria (or that at least the randomization will be postponed), the intent of the eligibility criteria is to ensure the subject was stable and on-going treatments well defined / stable at the time of randomization. •. It is mainly referring to diuretics and vasoactive substances or vasopressors. •. A change in a KCI perfusion would NOT be considered a violation. •. Nonetheless, the administration of albumin would be considered as a deviation and a contra-indication to randomization because of osmotic repercussions.’
‘The rule of the common law is, that where a party sustains a loss by reason of a breach of contract, he is, so far as money can do it, to be placed in the same situation, with respect to damages, as if the contract had been performed.’
‘It is important also to understand that the mere incurrence of expenditure does not in and of itself give rise to a loss sounding in damages. Under the so-called reliance measure, the critical further component, which converts the expenditure into a potentially recoverable loss, is that this has been wasted or rendered futile by reason of the breach.’
‘[A claim for wasted expenditure] has validity only if and to the extent that the Court is satisfied that the claimant would indeed have generated the necessary revenue to recoup the expenses. The Court will not knowingly make an award of damages which puts the claimant in a better position than if the contract had been performed and so will not allow a claim for wasted expenditure if the result of the breach is that the claimant has thereby managed to extricate itself from a loss-making transaction.’
‘To establish a bad bargain in such a case, the defendant would have to show that the value of the asset or other performance promised was less than the expenditure incurred by the claimant.’