A multi-center, adaptive, randomized, platform trial to evaluate the effect of repurposed medicines in outpatients with early coronavirus disease 2019 (COVID-19) and high-risk for complications: the TOGETHER master trial protocol [version peer review: 2 approved with reservations]

Background: Although vaccines are currently available for coronavirus disease 2019 (COVID-19), there remains a need for an effective and affordable outpatient treatment for early COVID-19. Multiple repurposed drugs have shown promise in treating COVID-19. We describe a master protocol that will assess the efficacy of different repurposed drugs as treatments for early COVID-19 among outpatients at a high risk for severe complications. Methods: The TOGETHER Trial is an international (currently in Brazil and Africa), multi-center platform adaptive randomized, placebo-controlled, clinical trial. Patients are is hospitalization due to clinical worsening of COVID-19 or emergency room required observation for more than 6 hours up to 28 days after randomization. Key secondary endpoints include viral clearance, clinical improvement, hospitalization for any cause, mortality for any cause, and safety and tolerability of each IP. Scheduled interim analyses are conducted and reviewed by the Data and Safety Monitoring Committee (DSMC), who make recommendations on continuing or stopping each IP. The platform adaptive design go-no-go decision rules are extended to dynamically incorporate external evidence on COVID-19 interventions from ongoing independent randomized clinical trials. Discussion: Results from this trial will assist in the identification of therapeutics for COVID-19 that can easily be scaled in low- and middle-income settings. The novel methodological extension of the platform adaptive design to dynamically incorporate external evidence is one of the first of its kind and may provide highly valuable information for all COVID-19 trials going forward. Thank you for asking me to review this manuscript which describes the protocol for a multi-agent platform trial of repurposed medications in the management of patients with early COVID-19. COVID has had a devastating effect on the world over the past 18 months, and although there is a growing armamentarium of pharmacological interventions, there remains potential for further improvements. In resource-limited settings, some of the therapies with proven benefit may not be available, and given the frequent use of repurposed medications in the management of patients with COVID-19 a trial of such interventions is highly warranted. My comments are as follows

is hospitalization due to clinical worsening of COVID-19 or emergency

Introduction
The discovery of effective and affordable treatments for preventing COVID-19 disease progression and subsequent hospitalization in outpatient settings is critical to minimize limited hospital resources, particularly for resource-limited settings 1 . As vaccine rollout has been slow in resource-limited countries and new variants of severe acute respiratory syndrome coronavirus 2 (SARS-CoV-2) cause concern for their effectiveness, identifying therapeutics that are affordable, widely available and effective against COVID-19 is of prime importance. Repurposing existing medications is an appealing approach as drugs currently used to treat other health conditions have known safety profiles.
There is also a need for more clinical trials in early infected populations. A majority of trials of repurposed drugs are conducted among inpatients with advanced clinical disease, yet the majority of COVID-19 cases are seen in the community setting 2 . Early treatment trials have the added benefit of evaluating drugs with the outcome of disease progression or hospitalization 3 . The TOGETHER Trial is an example of a global study network to evaluate repurposed drugs in early infected populations.
The TOGETHER Trial is an adaptive, multi-arm platform trial, evaluating multiple concurrent interventions (investigational products [IPs]) versus placebo among outpatients at high risk of developing COVID-19-related complications. The trial is designed to allow for multiple intervention arms to be implemented at any time and data to be merged with data from other external trials. This is a new approach for clinical trials that has occurred as a result of the COVID-19 pandemic and integrates platform adaptive trial designs with data synthesis to facilitate rapid decision-making. The overarching objective of this study is to test the hypothesis that repurposed drugs versus placebo effectively prevent worsening of COVID-19 requiring hospitalization or emergency room observation for greater than 6 hours among high-risk adults at 28 days post-randomization. This protocol is reported in line with the Standard Protocol Items: Recommendations for Interventional Trials (SPIRIT) guidelines 4 .

Study overview
The TOGETHER Trial is an adaptive, multi-arm platform trial with equal allocation of interventions and placebo. The setting for the trial is 10 primary care and emergency department outpatient clinics in the Brazilian state of Minas Gerais.

Objectives
The primary objective is to determine if each of the IPs reduces: 1) Emergency room visits due to the clinical worsening of COVID-19 (defined as participant remaining under observation for > 6 hours) within 28 days of randomization; 2) Hospitalization due to the progression of COVID-19 (defined as worsening of viral pneumonia) and/or complications within 28 days of randomization.
The secondary objectives are to evaluate, in comparison with placebo, the effect of the IPs on the following parameters: • All-cause, respiratory, and cardiovascular death • Viral clearance and viral load on day 3 and 7 after randomization (conducted the first 150 randomized participants) • Number of days with respiratory symptoms since randomization • Time between the start of treatment until the need for hospitalization/urgent care due to the progression of COVID-19 • Rate of all-cause and COVID-specific hospitalizations • Adverse events, adverse reactions to the study medications, and the proportion of participants who are adherent with the medications will also be assessed

Ethical considerations
Ethical review for this trial follows the Brazilian standard process of CEP/CONEP approval. The trial protocol is first reviewed by the local ethics review board in Brazil, followed by review at the national level by the National Committee for Ethics in Research (CONEP), since the trial is supported by international funding. CONEP approval number: 41174620.0.1001.5120. Research staff members located at the primary care or emergency department clinic where patients first present with symptoms are responsible for obtaining written informed consent. Prospective participants are read the informed consent form which describes trial procedures, potential risks, measures to protect their personal identity, and which parties will have access to their medical information. 19. Inability to follow protocol-related procedures.

Screening
Patients presenting to an outpatient clinic setting with clinical criteria for presumptive diagnosis of COVID-19 who meet the above eligibility criteria are invited to participate in the trial. Nurses, clinicians and health workers will obtain written informed consent from potential trial participants. After obtaining informed consent, research personnel collect demographic information and medical history, and confirm positivity for SARS-CoV-2 using the Abbott Panbio rapid antigen testing for previously undiagnosed patients.

Randomization and allocation
Participants are randomly assigned with equal allocation using a pre-generated randomization list based on block sizes of 8. The block sizes may be increased or decreased depending on the number of active treatment arms. Allocation of participants to treatment arms is uniform across all concurrent interventions as well as placebo. Treatment allocation occurs using a central WhatsApp number where study staff text blocking criteria (e.g. age and co-morbidities) and an unblinded pharmacist replies to the message within 5-10 minutes with the medication letter and randomization number.
Different placebos may be used depending on which IPs are included. For example, if IPs are being administered in both pill format and by injection, participants randomized to the placebo group will be randomly assigned to receive a placebo pill or a placebo injection. If IPs of different duration are being used (e.g. 1 day, 3 days, 10 days, 14 days), participants randomized to the placebo group will be randomized to different placebo durations or regimens.
The randomization is stratified by clinical site and by age (<50 years vs. >=50 years). The randomization sequence for each clinical site is prepared by the unblinded study pharmacist at each participating clinical site. Allocation of treatment assignment is concealed from all other study personnel.

Blinding
Randomization information is kept confidential by an unblinded statistician. Data are unblinded at the time of the planned interim analyses and at the end of the trial. The trial is quadruple blinded, with participants, research personnel, sponsors, and designees. The Data and Safety Monitoring Committee (DSMC) do not have access to the patient's allocation during review of the interim analysis data, except in the foreseen situations (i.e., decision to stop a treatment arm, termination of the trial, or safety concerns).

Investigational products
The master protocol format and the adaptive design allows the easy addition of different IPs. Ethics approvals are obtained before adding a new IP. Participants are prescribed the IPs and corresponding placebo as indicated in the protocol. An unblinded pharmacist at each clinical site prepares the IP or placebo as per the randomization sequence. The IPs are shipped and stored in a temperature-controlled manner as per the requirements for each IP. Table 1 shows the previous, current (at the time of writing), and planned IPs of investigation in the TOGETHER Trial.
Data entry and quality checks Study data are collected on a paper record by the study staff member either in-person at the clinic or by WhatsApp video or voice call with the participant. Data are entered into the IBM electronic case report forms (eCRFs) at each study site. Data quality checks are first performed at the site level, and secondary data checks are performed by central research staff, located at the research coordinating office in the Minas Gerais capital of Belo Horizonte. Weekly meetings are held by Zoom with all study sites to provide feedback on data quality and completeness and continuous training is provided to each site following any changes to the eCRFs or other study procedural amendment. The CRFs can be found as Extended data 4 .

Study outcomes
The primary outcome of the trial is a composite of 1) emergency room visits due to the clinical worsening of COVID-19 (defined as participant remaining under observation for > 6 hours) and 2) hospitalization due to the progression of COVID-19 (defined as worsening of viral pneumonia) and/or complications.
Secondary outcomes include: 1) viral clearance and viral load, 2) time to clinical improvement, defined as the first day on which the participant reports a score of 0 on the WHO Clinical Worsening Scale, 3) number of days with respiratory symptoms since randomization, 4) time to hospitalization for any cause, 5) time to hospitalization due to COVID-19 progression, 6) all-cause, cardiovascular, and respiratory death and time to death from any causes, 7) WHO clinical worsening scale scores over the follow-up period, 8) WHO clinical worsening scale scores during the treatment phase, 9) health-related quality of life (PROMIS global health scale ("Global-10"), and, 10) cognitive status (Telephone Interview for Cognitive Status [TICS]). Adverse events, adverse reactions to the study medications and the proportion of participants who are non-adherent with the study drugs will also be assessed. All secondary outcomes are assessed up to 28 days following randomization.
The study activities for capturing these outcomes at each visit is displayed in Table 2 and Figure 1.

Participant follow-up procedures
All participants receive standard treatment for COVID-19 as adopted by the health units to which they are linked, as defined by the medical assistant team. All participants will also receive 24-hour telephone contact number which they can call if they have any questions about the trial, if their condition worsens, or if they experience an adverse event. Participants will self-collect nasal swab and saliva for RT-PCR on day 3 and day 7 after randomization. Participants are instructed on this home sample collection and on the logistics for sample retrieval from their residence by study personnel.
The majority of patient evaluations are carried out by telephone contact, social media apps (e.g. WhatsApp), video calls or telemedicine. Face-to-face visits are limited as the virus is highly transmissible. Participants will follow the local health authorities' guidelines regarding isolation and quarantine requirements, which are generally 14 days from a positive COVID-19 test. Only the day-14 visit will be conducted face-to-face to enable study personnel to collect the medication kits for drug accountability and treatment compliance.
A number of procedures are implemented to maximize participant retention. An informative video recorded by the principal investigator and take-home flyer encourages patients to adhere to study procedures and complete the trial. Participants are also sent occasional notification reminders on WhatsApp encouraging trial participation and follow-up appointments by WhatsApp are conducted in an effort to minimize travel days to the clinic.
By Brazilian regulations, we provide medical care to all patients throughout their participation (2 months). For longer term events, the trial insurance covers any study related adverse event for a period of three years post-randomization. Auditing of the trial occurs at the central level with 50-60% Source Data Verification (SDV).

Trial committees
A Steering Committee and an independent DSMC have been established. The Steering Committee oversees the study to ensure scientific integrity and routinely assess emerging evidence to recommend interventions of interest for the trial. The DSMC oversees the safety of the research participants and reviews the results of each interim analysis and final analysis and makes recommendations on stopping or continuing each IP. Events of special interest flagged by the DSMC are followed-up by study physicians.

Sample size
Our trial applies sample size reassessment according to observed events. The trial is a platform adaptive trial design with three Table 2. Schedule of study activities.

± 5 days
Informed Consent X SARS-CoV-2 Rapid Test X (1) Eligibility Criteria Review X (2) Pregnancy Test Demographics X (5) Co-morbidities and Risk Factors Discontinue if significant symptoms or adverse reactions. 2. Screening and randomization (baseline visit) must be performed on the same visit. Ensure that the patient is randomized when at medical care facility. Patient with confirmed SARS-CoV-2 positive test and less than 7 days of symptom onset can be considered for randomization. 3. Subsequent visits: D3, D7, D10, D14, D28, D60 will be carried out by primarily by telephone and/or social media App. Extra visits for safety purposes can be made at any time. Visits D14 and D28 are considered outcome visits as per protocol. D60 is considered post-study visit for monitoring late complications related to COVID-19 and eventual evaluation of late adverse reactions to research drugs and will be carried out by telephone. There is no provision for face-to-face visits in this research in view of the regulatory recommendations issued by the public health authority in the context of the pandemic. 4. Daily contact by phone (not marked above) will be made between Days 1 to 7. Phone contact after D7 will be performed as per protocol. COVID-19=coronavirus disease 2019, SARS-CoV-2=severe acute respiratory syndrome coronavirus 2.
planned interim analyses at approximately 25%, 50%, and 75% of the total required sample size. The initial sample size calculation is based on the test for the hypothesis that each of the IPs will be better than placebo in reducing the risk of hospitalization and emergency room care at least 6 hours in duration due to complications directly related to COVID-19. The sample size of 681 patients per arm was chosen for each experimental group to achieve 80% power with 0.05 two-sided Type 1 error for a pairwise comparison against the control to detect minimum treatment efficacy defined by 37.5% relative risk reduction (RRR) of preventing hospitalization assuming a control event rate (CER) of 15%. The sample size calculation will be revised based on the outcomes that occurred during the interim analyses. Blind analysis of outcomes with simulations will be conducted to limit type I errors within the 5% tolerance range (97.5% or greater probability of superiority over the control group). Individual treatment arms can be stopped if there are no acceptable projections of benefit at the expense of futility.

Interim evaluations
Interim efficacy analyses are scheduled. Assuming a uniform prior assigned to the different event rates, a total sample size of 681 patients per arm, a CER of 15%, and a RRR equals to 37.5%, an interim analysis will be performed after observing approximately 25%, 50% and 75% of the maximum number of patient outcomes, as well as at the trial completion. The posterior efficacy threshold to stop for superiority is 97.6% and the futility threshold is 20%, 40% and 60% at the respective interim analyses. Intervention arms(s) showing a posterior probability of efficacy crossing either boundary, will be stopped for either reason. These superiority and futility thresholds were determined based on 200,000 simulation run ins wherein different values of the RRR were considered (0%, 20%, and 37.5%). A description of this interim analysis in an event-based Bayesian adaptive trial and accompanying illustrating example can be found in the appendix of this document.
When other data from other relevant studies become available, we will use Empirical Bayes meta-analysis 5 to borrow information from the treatment effects or safety signals emerging from these studies. This is effectively a random effect Bayesian model that results in simultaneous shrinkage of the treatment effect or safety estimates reported in the various studies toward the meta-analysis estimate, while still providing standalone estimates. Schoenfeld et al. have shown 6 that this approach is, in some ways, equivalent to the power prior approach of Chen and Ibrahim 7 , whereby historical studies are assigned fractional weight(s) whose magnitudes correspond to the consistency of their data with that of the study they are thought to inform. The analyses incorporating external evidence will be presented to the DSMC as secondary findings to consider but will not alone trigger a recommendation for a trial adaptation.

Statistical analyses
A detailed description of the TOGETHER Trial statistical analysis plan can be found in the Extended data 4 .
In brief, the efficacy of each intervention will be analyzed in terms of its posterior efficacy with respect to placebo, using the Bayesian paradigm, while calibrating the decision boundaries to meet the type I error rate requirements. We will adopt an intention-to-treat principle to analyze all results. Multiple imputation will be employed where statistical models require adjustment for baseline covariates with up to 20% missing values. No multiple imputation of outcomes will be performed.
We will use Bayesian inference for dichotomous outcomes, adjusting for covariates when necessary. Similarly, we will validate the proportional hazards assumption by visually inspecting Kaplan-Meier and log-negative-log of survival plots and fit Cox model for time-to-event outcomes. Secondary outcomes, such as viral clearance will be modelled using a longitudinal logistic model with a subject random effect, using the PCR test result over time as our dependent variable.

Subgroup analyses
We will perform subgroup analyses to assess the consistency of effects in four patient subgroups: • Age: ≥50 years or <50 years We hypothesize that younger patients will benefit more than older patients, women will benefit more than men, patients with an earlier diagnosis will benefit more than those with a later diagnosis, and patients without the clinical co-morbidities described above will benefit more than those with these co-morbidities. All the subgroup hypotheses are based on data emerging from other countries, indicating the differential impact of COVID-19 by age, sex and the existence of clinical comorbidities at baseline conditions. Data from the IBM eCRFs are securely sent by File Transfer Protocol (FTP) to the statistical team in SAS format. SAS v9.4 is used to convert raw data into an analytic dataset applying CDISC standards. Analyses are conducted using R v4.0.3. Results will be reported following the CONSORT guidelines.

Role of the funding source
The funder of this trial had no role in study design, data collection, decision to publish, or preparation of the manuscript.

Dissemination of study findings
The final trial dataset will be accessible by written request to the study principal investigators (G Reis or EJ Mills). There are no contractual agreements to limit access to final trial data. All data collected by the TOGETHER Trial will be shared with the International COVID-19 Data Alliance. Access to these data through the ICODA Workbench will follow the standard operating procedures developed by the ICODA working group.
Findings will be disseminated in several ways. All investigations of IPs vs. placebo will be submitted to an appropriate, peer-reviewed scientific journal. Lay summaries of findings will be made available on the TOGETHER Trial website (togethertrial.com). The investigative team is also connected to the WHO COVID-19 guidelines committee, where trial findings will help inform global clinical guidance.

Study status
The TOGETHER Trial has recruited more than 3000 patients to date. The trial has previously evaluated the effect of hydroxychloroquine or lopinavir/ritonavir on risk of hospitalization 8 . An arm evaluating metformin vs. placebo was stopped early by the DSMC for futility. Other arms evaluating ivermectin and fluvoxamine are continuing. Future planned evaluations will include doxazosin and pegylated interferon lambda. The IPs of investigation in the TOGETHER Trial and their study status at the time of writing is further described in Table 1.

Discussion
Our TOGETHER trial is innovative in a number of ways. First, from a clinical perspective, we are examining the use of drugs that would be widely available and accessible if proven effective and safe for the treatment of COVID-19. Second, our trial uses a new methodological approach adaptable to both internal accumulating data, as is common in platform trials, as well as incorporate external trial evidence that may be unplanned at the time of initial study launch.
Currently, there are no effective approved therapeutic interventions approved for the early treatment of SARS-CoV-2 1,9-11 . Proposed therapies for SARS-CoV-2 are based on previous clinical experience directed against SARS-CoV-1 and Middle East respiratory syndrome (MERS) 12 . These therapeutic modalities consisted of viral methyl transferase inhibitors, protease inhibitors, interferon, inhibitors of viral ribonucleic acid (RNA) synthesis as well as anti-inflammatory drugs. For the treatment of COVID-19, there has been much promise and excitement for repurposing drugs that have similar targets described for SARS-CoV-1 and MERS 1,13 . The current use of repurposed drugs for COVID-19 treatment offers several key advantages as these medicines have been proven safe, their pharmacokinetics are well understood, and optimal dosages are standardized. Although hydroxychloroquine is ineffective for the treatment of COVID-19 among hospitalized adults 14 , other repurposed drugs have already shown promise against COVID-19 disease at the later stages of disease. Both dexamethasone and tociluzimab appear to significantly increase survival accordingto findings from the UK RECOVERY trials 15 . Furthermore, other new molecules such as remdesivir and monoclonal antibodies have had inconsistent findings 16,17 . Unfortunately, well-designed studies on asymptomatic or mild, or pediatric cases of COVID-19 are lacking. Neither hydroxychloroquine nor lopinavir-ritonavir showed any significant benefit for decreasing COVID-19-associated hospitalization or other secondary clinical outcomes in early symptomatic COVID-19 patients 8 . In a preliminary study of adult outpatients with early COVID-19, patients treated with fluvoxamine, compared with placebo, had a lower likelihood of clinical deterioration over 15 days 18 . In another recent trial of favipiravir, an RNA-dependent RNA polymerase inhibitor, also did not show any statistically significant benefit in term of mortality in the general group of patients with mild to moderate COVID-19 19 . It was suggested that the use of antivirals in symptomatic patients is too late and would explain their low efficacy in the clinical setting. A number of clinical trials (NCT04426695, NCT04425629, NCT04479631) have now been initiated to assess safety, tolerability, and efficacy of SARS-CoV-2 neutralizing monoclonal antibodies (nMAbs) using either a prophylactic or therapeutic approach 20-22 . In addition, potent human monoclonal antibodies against SARS-CoV-2 have been isolated from COVID-19 convalescent patients which could provide another layer of therapeutic options against the disease 23 . Thus, by blocking acute virus replication, early nMAb intervention would potentially induce a better clinical outcome against COVID-19.
Our study has several limitations. Perhaps the greatest limitation of our study is that the administrative stages of conducting a trial, from protocol development and ethics review to obtaining study drug and creating electronic case report forms are all reliant on the local infrastructure and norms of study conduct in those settings. Our adaptive elements of the trial complicate what is understood by some agencies and push-back from approval bodies has previously delayed enrolment. The rapid change in the scientific interest or confidence in interventions means that an application submitted to a funding agency or ethics committee, may, by the time it is reviewed, have changed dramatically. Strengths of our study include the adaptive nature of the study to change arms by dropping or adding arms as the data, both internal and external. Our design permits outside data, from either trial we already collaborate with or trials with emerging data we learn of as we are conducting our trial. Similarly, outside evidence in the form of completed trials, may provide sufficiently compelling evidence to change the direction of our trial or change outcomes and interpretation of trial findings.
Our design is adaptive and also Bayesian in its learning structure and analysis. We refer to this as a learning structure as emerging data from our own trial will, almost certainly be influenced from data we were unaware of at the study outset. We are already learning of similar trials examining similar interventions (in at least one arm) where the population inclusion criteria and the outcomes can be harmonized with our dataset. Similarly, we may find out about completed trials that have convincing evidence that mandates a change in our trial. For example, if a large study with a similar population and outcome found overwhelming evidence of a treatment effect (whether that is harm, futility, or benefit), we may examine our data to confirm that the direction of treatment effect is similar. This may take the form of matching the population using a strategy such as propensity scoring or combining in a meta-analysis.
Results from this trial will help identify repurposed therapeutics for COVID-19 that can easily be scaled in low-and middle-income settings. The novel methodological extension of the platform adaptive design to dynamically incorporate external evidence will be the first of its kind and may prove highly valuable for all COVID-19 trials and trials for other indications going forward.

Data availability
Underlying data No data are associated with this article. Severe degenerative neurological disease or psychiatric disease are again vaguequantification of functional impairment, or in case of psychiatric disease requirement for psychiatric hospitalisation, or indication of specific diagnoses may make these more objective.
The inclusion of placebos is worthy of commendation -this has not been used in previous multi-platform trials, and the use of variable placebos in line with the agents being included is a novel and innovative approach to this issue and is to be commended.

7.
It is unclear how the trial drugs included have been selected or what process is in place for review and selection. Although several drugs included are those with established in-vitro antiviral activity (e.g. hydroxychloroquine, Lopinivir/ritnovir) both these have been subjected to large RCT assessment without any evidence of benefit, all-be-it in either more severe patients or in prophylaxis. Review of the existing literature, criteria for selection and rationale for each agent selected should be included. Rationale for the dose and dosing interval selected should also be included. The protocol authors rightly indicate that their trial is adaptable and will be informed by external trial results, but in the proposed initial medication this is not immediately apparent. 8.
The previously published results of the HCQ, ritnovir/lopinavir (JAMA Network 2021) appear to show, with a different end-point (hospitalisation only) no benefit, it is unclear why they are included in this protocol as they are not being judged against the same endpoint as published here? 9.
The power calculation assumes at 15% event rate, however the authors previous iteration of this study comparing HCQ, ritnovir/lopinavir and placebo (JAMA network open, 2021) had an event rate of 5% for hospitalisation. Do the authors have any data to indicate that the control group event rate of hospitalisation and prolonged ER stay is likely to be 3x higher than hospitalisation alone? The 37.5% relative risk reduction, corresponding to a 5.6% absolute risk reduction does seem fairly generous, and it would be helpful to know how that value had been selected (prior data, minimum clinically beneficial response?)

10.
Response: We have deleted this exclusion criteria as we agree that is it is redundant with inclusion criteria 2.
5. The definition of moderate to severe liver disease is unclear, sticking to Childs-Pugh C alone (or a lower C-P cut-off) would make this more objective.
Response: As suggested by reviewer #1, we have removed this criteria and replaced it with the following: severe terminal illness irrespective of type or etiology.
6. Severe degenerative neurological disease or psychiatric disease are again vaguequantification of functional impairment, or in case of psychiatric disease requirement for psychiatric hospitalisation, or indication of specific diagnoses may make these more objective.
Response: As suggested by reviewer #1, we have removed this criteria and replaced it with the following: severe terminal illness irrespective of type or etiology.
7. The inclusion of placebos is worthy of commendation -this has not been used in previous multi-platform trials, and the use of variable placebos in line with the agents being included is a novel and innovative approach to this issue and is to be commended.
Response: Thank you for the positive feedback.
8. The previously published results of the HCQ, ritonavir/lopinavir (JAMA Network 2021) appear to show, with a different end-point (hospitalization only) no benefit, it is unclear why they are included in this protocol as they are not being judged against the same endpoint as published here?
Response: The composite endpoint addresses both hospitalization and a proxy for hospitalization, retention in a COVID-19 emergency setting, as many patients who would be hospitalized were prevented from admission due to hospital over-capacity during peak waves. This region of Brazil implemented hospital-like services in the emergency settings with 50-80 bed settings and providing services including oxygenation, sedation, multi-day stays, and mechanical ventilation. We have added the above text to the manuscript.
9. The power calculation assumes at 15% event rate, however the authors previous iteration of this study comparing HCQ, ritonavir/lopinavir and placebo (JAMA network open, 2021) had an event rate of 5% for hospitalization. Do the authors have any data to indicate that the control group event rate of hospitalization and prolonged ER stay is likely to be 3x higher than hospitalization alone? The 37.5% relative risk reduction, corresponding to a 5.6% absolute risk reduction does seem fairly generous, and it would be helpful to know how that value had been selected (prior data, minimum clinically beneficial response?) Response: Thank you, assuming an excessively high CER has been detrimental to our purposes in the past. However, the event type we use these days has been shown to have a much higher CER (see our response to comment #4 of reviewer #1).
The authors have done a masterful job in many aspects. They are addressing a very prominent global health problem, namely outpatients with early coronavirus disease 2019 (COVID-19) and high risks of complications. They are assessing large numbers of interventions (to be decided) that may have a potential to benefit the course of disease and prevent complications. The authors are doing so in an international collaboration employing an adaptive platform trial structure with decentralized randomization by study pharmacists using centralized pre-generated randomization with variable block sizes. The randomization is stratified by clinical site and participant age (less than 50 years or more). The protocol promises placebo controls, an important advancement compared to many other current platform trials. The adaptive platform trial conducts novel analysis plans for the accumulating data combined with external trial evidence. The team of authors covers many experienced trialists, methodologists, and statisticians, which heralds high chances of success in conducting this complex adaptive platform trial. This is really a clinical research project that significantly may help to guide future treatments for such outpatients.
We have also some comments and points that we think should be addressed more in the protocol and/or SAP to become clearer as well as some points where this platform trial could consider adapting some of our suggestions. These comments and points are as follows: Investigational products: Considering the pressures for getting access to just something that could work against COVID-19 infection (e.g., chloroquine; ivermectin; bleach; etc.), we suggest the screening for interventions for this trial could maybe become a bit better described and organised? Why not center such screening around living systematic reviews of interventions for hospitalised patients with COVID-19 as well as for outpatients with COVID-19 (both less affected and as affected as the present cohort of participants)? As the patients going to be entered into the TOGETHER trial have been less well examined, ideas for interventions for this type of patients will likely come from other patient groups or similar patients but with less or more disease severity.

Sample size estimation:
We think the issue of sample size estimation needs reconsideration, discussion, and possible adaptation. The start intervention effect of a relative risk reduction (RRR) of 37.5% seems unrealistically high for most interventions directed at this condition and outcome. There will be risks of both stumbling over larger effects (type I errors) or smaller effects (type II errors) when the trial has low accrued sample size and these may lead to erroneous decisions and conclusions.
As we are speaking often of repurposed drugs as experimental interventions, why not use the meta-analytic intervention effects to guide decisions of choice of RRR, often in the range of RRR of 5% to 15%? You seem to suggest this in 4.3.2 of your SAP, but it has not been adapted?
You address sample size re-estimation in 4.3.1 of the SAP, but we are bewildered as the methodology is not described in any detail and the heading states that this only deals with Brazil? We suggest these central aspects need detailed description in the SAP as well as clear mention and description in the article proper.
The control event proportion (CEP) chosen as 15% also seems too high. In your own publication of results from the TOGETHER trial, the placebo group had a CEP of 4.8% (Reis et al., 2021 1 ); despite the small number of patients and associated uncertainty, the planned sample sizes may thus be too small for this proportion. Adaptation of realistic CEP for future sample size estimations will increase the demands for participants, but the problem in the world is not difficulties finding COVID-19 infected people. The type II error chosen is on the low side being only 80%. Would 85% not be more correct considering your own results in Appendix 1 of your SAP and the prominence this trial will likely achieve?

Exclusion criteria of participants:
Considering that you are dealing with outpatients where time constraints limit the possibilities for conducting in depth differential diagnostic activities, would it not be simpler and just as effective to condense or delete the following exclusion criteria: 4. Why have this at all? ○ 5, 10, 11, 13, 14, 15, 16, which could be condensed into something like: severe terminal illness irrespective of type or etiology.

○
The substantial number of exclusion criteria limit the external validity to the full population of patients that may get treated with the assessed interventions somewhat, and exclusion of patients with several comorbidities may explain the lower than expected CEP. This may warrant further discussion in the manuscript.

Is the rationale for, and objectives of, the study clearly described? Yes
Is the study design appropriate for the research question? Partly

Are sufficient details of the methods provided to allow replication by others? Partly
Are the datasets clearly presented in a useable and accessible format? Not applicable Competing Interests: No competing interests were disclosed.
We confirm that we have read this submission and believe that we have an appropriate level of expertise to confirm that it is of an acceptable scientific standard, however we have significant reservations, as outlined above.
Author Response 20 Oct 2021

Edward Mills, McMaster University, Hamilton, Canada
Investigational products: 1. Considering the pressures for getting access to just something that could work against COVID-19 infection (e.g., chloroquine; ivermectin; bleach; etc.), we suggest the screening for interventions for this trial could maybe become a bit better described and organised? Why not center such screening around living systematic reviews of interventions for hospitalized patients with COVID-19 as well as for outpatients with COVID-19 (both less affected and as affected as the present cohort of participants)? As the patients going to be entered into the TOGETHER trial have been less well examined, ideas for interventions for this type of patients will likely come from other patient groups or similar patients but with less or more disease severity.
Response: Thank you for the comment. Investigational products tested for the TOGETHER Trial were carefully chosen by an international collaboration of pharmacological experts, clinicians, previous RCT's and an extensive literature search across multiple databases.

Sample size estimation:
2. We think the issue of sample size estimation needs reconsideration, discussion, and possible adaptation. The start intervention effect of a relative risk reduction (RRR) of 37.5% seems unrealistically high for most interventions directed at this condition and outcome. There will be risks of both stumbling over larger effects (type I errors) or smaller effects (type II errors) when the trial has low accrued sample size and these may lead to erroneous decisions and conclusions. As we are speaking often of repurposed drugs as experimental interventions, why not use the meta-analytic intervention effects to guide decisions of choice of RRR, often in the range of RRR of 5% to 15%? You seem to suggest this in 4.3.2 of your SAP, but it has not been adapted?
Response: Thank you for your great question. There is a balance to be found here between our quest to finding effective treatments, the magnitude of the effects, and the resources required to determine the efficacy of said treatment. A 5-15% RRR treatment is both limited in its efficacy and hugely taxing in terms of the number of patients it would require, deeming it not worthy of investment. Our judgement was that around 30% RRR would represent a good working point.
3. You address sample size re-estimation in 4.3.1 of the SAP, but we are bewildered as the methodology is not described in any detail and the heading states that this only deals with Brazil? We suggest these central aspects need detailed description in the SAP as well as clear mention and description in the article proper.
Response: Thank you. We have now added the following text: "Sample size re-assessment will be performed, subject to the DSMC's approval, if after the third interim analysis the control event rate appears to be considerably lower to the one the original sample size calculation was based on, irrespective of the observed RRR. In that event, we will rerun the simulation based on the new sample size calculated and with the first three interim analyses taking place as originally planned, to confirm that no type I error rate inflation is occurring. Should the efficacy criterion at the final analysis be modified to ensure that, any further change to the original design will be documented and reported." 4. The control event proportion (CEP) chosen as 15% also seems too high. In your own publication of results from the TOGETHER trial, the placebo group had a CEP of 4.8% (Reis et al., 2021 1 ); despite the small number of patients and associated uncertainty, the planned sample sizes may thus be too small for this proportion. Adaptation of realistic CEP for future sample size estimations will increase the demands for participants, but the problem in the world is not difficulties finding COVID-19 infected people. The type II error chosen is on the low side being only 80%. Would 85% not be more correct considering your own results in Appendix 1 of your SAP and the prominence this trial will likely achieve?
Response: Thank you for your question. This is the same issue addressed in our last response. We will comment that we have learned our lesson from the early TOGETHER trial, and evidently, the CER in the latest iteration of the trial has been almost spot on the expected 15%.

Exclusion criteria of participants:
5. Considering that you are dealing with outpatients where time constraints limit the possibilities for conducting in depth differential diagnostic activities, would it not be simpler and just as effective to condense or delete the following exclusion criteria: Response: Thank you for a great point raised. Indeed, response adaptive randomization could increase the power of the trial, if the goal is finding the most effective treatment among multiple active treatment. However, here we are interested in finding all effective treatments, therefore all test performed will involve control comparisons. Because the arms are not 100% overlapping, we need to confirm that each of them is compared to sufficiently many controls. To warrant that without planning on non-concurrent control borrowing, we have to apply 1:1 randomization ratio.

Trial outcomes:
9. According to 4.3.4 at page 23 of the SAP, you intend to conduct a follow up interview at day 60. Why not use this data to assess more 'long-term' mortality as well?
Response: We have revised the SAP to also look at long-term mortality[SS1] .

Data Monitoring and Safety Committee:
10. Why is this committee not independent? Professor Thorlund is Vice President of the contract research organisation (CRO, i.e CYTEL), employee of the CRO, professor at the sponsoring university, author of the TOGETHER protocol, and member of the DMSC for the trial. Dr Haggstrom also seems connected to the CRO? And why is this committee not blinded?
Response: We have corrected the membership of our DSMC and clarified that Professor Thorlund serves as the non-voting chair of the DSMC.

Statistical analysis:
11. Missing data handling: the authors plan to use multiple imputation for baseline covariates with up to 20% missing values, with no imputation of outcome variables. This description is very sparse and could be expanded. Which imputation method will be used? How many imputations will be performed? Which variables will be included in the imputation models?
Response: Thank you for your question. The following text was added to the SAP: "For descriptive statistics, multiple imputation will be employed where baseline covariates with up to 20% missing values among age, sex, race, BMI, time since disease onset and comorbidities, using the Multiple Imputation by Chained Equations (MICE) algorithm (van Buuren & Groothuis-Oudshoorn, 2011). However, adjustment to covariates -and subsequent pooled -analysis in the outcome model will only include covariates whose distribution appears to be imbalanced across the treatment arms." 12. Prior choices: the authors plan to solely use flat priors. This is a convenient and reasonable choice, but it is often recommended to 1) justify prior choices and 2) consider sensitivity analysis using different priors (Sung et al., 2005 3 ). Could the authors comment on this?
Response: Thank you for this thoughtful comment. While we agree with the general premise, we expect fairly large samples and number of events, therefore the chosen prior is unlikely to have much impact, and the convenience of using uniform priors is also likely to be received better by Bayes-skeptics. In fact, our results (e.g., point estimates and credible intervals) agree with standard frequentist analysis almost perfectly.
13. The authors plan to use Markov chain Monte Carlo methods we, but do not specify how chain convergence/model fit is going to be assessed. This is generally recommended (Sung et al., 2005 3 ) and should be added to the SAP.
Response: To make it clear, Markov Chain Monte Carlo sampling will only ever be used in the rare event that adjusted analysis is required, in which case we will be using Stan, i.e., Hamiltonian Monte Carlo. We have added the comment and reference to the SAP.
14. The authors write: "We will use Bayesian inference for dichotomous outcomes, adjusting for covariates when necessary." More details seem necessary -while adjustment for relevant, pre-specified covariates is generally recommended in clinical trials (to increase power and handle potentially important baseline imbalances), the adjustment strategy should ideally be pre-specified. Which co-variates will the author adjust for? When will it be considered "necessary"? Will the authors adjust for the stratification variables, as is generally recommended in stratified trials (Kahan and Morris, 2012 4 )? Ideally, the full model should be specified a priori.
Response: Thank you for this important comment. This issue has now been addressed in the response (and the corresponding added text) to comment number 12.
15. The authors plan to incorporate external data using an empirical Bayes individualparticipant data meta-analysis. This strategy appears sound -however, the authors write that this will be done if individual-participant data becomes available. Most trials (for data sharing/privacy reasons) do not share individual-participant data openly, and when done, this is usually after a substantial delay. Are the authors planning to contact relevant trials to obtain individual-participant data or is there another strategy for this in place? If not, it seems relatively unlikely that this will be possible, and then a bit less sophisticated but possibly practically more feasible strategy could be the inclusion of meta-analysed trial-level data in the analysis. Could the authors comment on this?
Response: Thank you. This is highly unlikely indeed. The cited paper makes no mention of IPD, and the inclusion of it in the text was erroneous. In any case, this will serve as merely a complementary analysis and not a primary one.
16. The individual-participant data meta-analysis is sparsely described, and further details would add substantial value. The authors write that they will use pseudo-informal variable selection, partially based on expert knowledge and on forward selection. This description is very vague and leaves a lot of room for "researcher degrees of freedom". Could the approach be described in greater detail? Which experts will be asked? How will the forward