Hydroxychloroquine versus placebo in the treatment of non-hospitalised patients with COVID-19 (COPE – Coalition V): A double-blind, multicentre, randomised, controlled trial
et al., The Lancet Regional Health - Americas, doi:10.1016/j.lana.2022.100243, NCT04466540, Mar 2022
Outpatient RCT with 687 HCQ and 682 control patients in Brazil, showing
lower hospitalization with treatment, not reaching statistical significance. Higher
efficacy was seen with treatment <4 days from onset, RR 0.60 (p = 0.15). The associated
meta-analysis includes mostly late treatment studies, for example in Schwartz et al.
the median delay from onset was 7 days. Omrani et al. is missing. The values for
Johnston et al. are incorrect - the study shows 4 hospitalizations in the control arm
- RR for this study should be 0.58 instead of 0.78.
This trial has multiple serious issues:
HCQ for COVID-19
1st treatment shown to reduce risk in
March 2020, now with p < 0.0000000001 from 424 studies, used in 59 countries.
No treatment is 100% effective. Protocols
combine treatments.
6,600+ studies for
220+ treatments. c19early.org
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CRITICALEvent adjudication committee not independent as registered.
The design paper and both trial registries state that the primary outcome would be centrally adjudicated by an independent committee. The supplementary appendix names the committee as two physicians from the coordinating centre who are both Steering Committee members and co-authors of the paper, one of them is the second author.
CRITICALClaim of zero loss to follow-up in 1,372 outpatients is implausible.
Authors state that no patients were lost to 30-day follow-up and that the primary outcome was fully ascertained in all 1,372 randomised patients. No follow-up procedure is described that could plausibly achieve this. The REBEC record describes primary-outcome assessment 'through telephone contact by a trained professional'. No contact-completion rate, scontact method cascade, or coding rule for unreachable patients is reported. Ascertainment could not have relied on enrolling-site records: several of the highest-enrolling centres have no inpatient capacity at all (ALPHACOR, Maestri e Kormann Consultoria Medico-Cientifica), and during the 2020-21 surges deteriorating patients were routed to whichever hospital had capacity, frequently in another city, while privately insured patients would be admitted within their own networks. Ascertainment therefore rested on reaching the patient or family. Additionally, the primary outcome appears to be the only variable in the dataset with no missingness.
CRITICALMortality hazard ratio not reproducible from the reported death counts.
Deaths are reported as 5/687 (HCQ) vs 5/682 (placebo) in ITT and 5/477 vs 5/470 in mITT, yet the Firth-penalised univariate Cox model returns HR 1.56 (0.42-6.72), p=0.540, and 1.55 (0.41-6.67) in mITT. This is not reconcilable with the published data. In a two-arm Cox model with ten events, no censoring, and risk sets of 687 vs 682, the partial likelihood is driven by the ratio of risk-set sizes rather than by event timing. Simulating maximally extreme separation - all five HCQ deaths on days 1-5 and all five placebo deaths on days 26-30 - returns HR 0.996; the reverse ordering returns 0.989; identical timing returns 0.993.
CRITICALImpossible mechanical-ventilation counts.
The binary outcome reports invasive mechanical ventilation in 8 HCQ and 6 placebo patients, but the duration-of-invasive-ventilation analysis includes 14 HCQ and 11 placebo patients. The same contradiction persists in the mITT analysis, with 8/6 ventilation events versus 14/10 patients with ventilation-duration data.
CRITICALNo response to data request.
Authors did not respond to a request for the data.
CRITICALMajor registered design changes after enrollment began.
The prospectively registered REBEC version dated April 8, 2020 describes a randomized pragmatic OPEN trial of HCQ versus control and limits enrollment to patients within 48 hours of symptom onset4. The later REBEC record changes the trial to DOUBLE-BLIND and PLACEBO-controlled and expands eligibility to <=7 days from symptom onset. The revised record is date June 2, 2020, while the registry records first enrollment on May 13, 2020. Therefore the public registry history shows material changes in masking, comparator, and treatment timing after recruitment had begun.
CRITICALInitial design with treatment ≤ 48hrs from symptom onset changed to ≤7 days.
As above, the original prospectively registered trial restricted treatment to ≤48 hours from symptom onset4, but this was later expanded to ≤7 days during the period in which HCQ became intensely politicized in Brazil. The change is material because the hypothesized direct antiviral effect is time-dependent and authors themselves state that potential HCQ benefit is most biologically plausible during early viral replication.
The change is expected to significantly reduce sensitivity to a benefit confined to early treatment - precisely the benefit hypothesized by authors.
Protocol versions 1-3 and their approval/implementation dates are missing, preventing determination of when, why, and by whom this major eligibility change was made. The timing is notable because the Health Ministry approached PI Álvaro Avezum in mid-May to fast-track this HCQ trial specifically in hopes that evidence on early intervention could resolve an escalating political dispute. Around the same time the Brazilian medical establishment and the AMIB/SBI/SBPT evidence panel adopted a negative stance.
CRITICALLimited symptom onset details; higher efficacy for patients treated within 4 days.
A breakdown for treatment within 4 days and later treatment shows improved results for earlier treatment, RR 0.60 (p = 0.15) vs. RR 0.85 (p = 0.49). Notably, no results are reported for the original trial design - treatment within 48 hours, and no breakdown is provided for mortality.
CRITICALPublished mITT definition differs from protocol.
The protocol defines mITT by excluding patients definitively confirmed negative for COVID-19, whereas the publication describes the prespecified mITT as consisting only of confirmed-positive patients.
CRITICALData shows improved results for earlier treatment - matching author expectations but with no discussion.
As above, results were more favorable with earlier treatment - RR 0.60 (p = 0.15) for <4 days versus 0.85 (p = 0.49) for ≥4 days, consistent with the authors' stated biological expectation that HCQ benefit would be more plausible during early viral replication. While this was not statistically significant given the number of events, it is notable that the paper does not discuss the magnitude or direction of this timing gradient, instead stating only that no significant subgroup interaction was detected.
CRITICALProtocol amendment history not supplied despite statement that it is.
The main text states that additional details on protocol amendment, DSMB role and interim analyses are provided in the supplementary appendix. The appendix supplies only protocol version 4.0 dated 5 October 2020. Versions 1-3, the amendment log and dated approvals are absent, as are DSMB reports.
CRITICALParticipant-flow and diagnostic counts do not reconcile.
Figure 1 reports 207 HCQ and 208 placebo participants with negative SARS-CoV-2 tests, while Table 1 reports only 197 and 194 negative tests, respectively, plus 14 and 18 participants with testing not performed.
CRITICALAllocation imbalance impossible under the randomisation method described.
689 vs 683 patients were allocated, an imbalance of 6. The protocol, ClinicalTrials.gov record and paper all describe a single centralised randomization in permuted blocks of eight, and the protocol explicitly rejects stratification. With one unstratified block-of-8 sequence, 1372 allocations give 171 complete blocks (684/684) plus one partial block of 4, so the maximum achievable imbalance is 4.
CRITICALMortality denominators conflict with complete follow-up claim.
Mortality is reported as 5/687 versus 5/682 despite randomization of 689 versus 683 and the manuscript stating that no patients were lost to 30-day follow-up.
CRITICALUnexplained safety-analysis denominators.
Serious adverse events are reported using denominators of 654 HCQ and 647 placebo despite 689 and 683 randomized participants and general adverse events being reported using the full randomized denominators.
CRITICALPrespecified unconfirmed-COVID sensitivity analysis not reported.
The protocol explicitly planned a sensitivity analysis comparing the primary endpoint in probable/unconfirmed COVID-19 cases with confirmed cases, but this analysis does not appear in the published results or supplementary results.
CRITICALNo excess of drug-typical adverse effects, inconsistent with hydroxychloroquine pharmacology.
Diarrhoea was 21.9% (HCQ) vs 22.4% (placebo) in ITT and 27.6% vs 28.0% in mITT; anorexia 7.9% vs 7.1%; total adverse events 24.2% vs 22.1%. An 800 mg loading dose reliably produces excess gastrointestinal symptoms, and the authors' own companion meta-analysis reports any-AE RR 1.78 across outpatient trials.
SERIOUSEligibility described as mild in protocol and registries but mild or moderate in the publication.
The protocol synopsis, ClinicalTrials.gov and REBEC all specify patients 'presenting mild symptoms' with no indication for hospitalisation. The publication describes the population as having 'mild or moderate' symptoms throughout, including in the title context, abstract, methods and conclusions.
SERIOUSRevised sample-size calculation does not maintain the claimed >=80% power.
The paper states that approximately 30% negative testing prompted additional enrollment to maintain at least 80% power for the mITT analysis and that the revised target was 1,620 participants. Under the trial's original assumptions of 20% versus 14% hospitalization, however, 1,620 randomised participants with 70% remaining test-positive yields only about 567 analyzable patients per arm and approximately 77% power, not >=80%.
SERIOUSBaseline imbalance for immunocompromise-related conditions; visible only in appendix.
Immunocompromise-related conditions are uniformly higher in the HCQ arm - active cancer 1.2% vs 0.2%, rheumatologic disease 1.7% vs 0.8%, chronic haematologic disease 0.6% vs 0.2%, HIV/AIDS 0.6% vs 0.2%, COPD 1.4% vs 1.0%. Immunosuppression was a qualifying eligibility risk factor but appears nowhere in Table 1, so this imbalance is visible only in the supplement and only for the test-positive subset.
SERIOUSOne registered secondary sub-outcome and all exploratory outcomes unreported.
The registered secondary endpoint 'time to improve respiratory symptoms (cough, runny nose)' is reported for cough only. The protocol's exploratory 12-month outcomes (survival, rehospitalisation, home ventilatory support, functional capacity, anxiety, depression, PTSD symptoms, return to work, quality of life) are not reported.
SERIOUSStated funder role contradicted by registry, supplement, and authorship.
The paper state that the trial was 'designed, overseen, and sponsored by the Coalition COVID-19 Brazil' and that EMS Pharmaceutical supplied the study drug but had no role in study conduct, statistical analyses, or the decision to submit the manuscript. However, the protocol identifies 'EMS and Covid-19 Brazil Coalition' as the Main Sponsor and separately states that EMS S.A. assumed sponsor responsibilities under Brazilian RDC 09/2015. The supplement also identifies two 'Representatives from EMS Pharma', and one of them is a study co-author and declared EMS employee.
MAJORHighly concentrated enrollment with no site-level outcome data published.
Supplementary Table 1 sums correctly to 1372 across 56 sites, but the top site contributed 248 patients (18.1%), the top 3 contributed 41.0% and the top 10 contributed 70.7%. Thirty of 56 sites enrolled fewer than 10 patients and six enrolled exactly one. No site-level outcome, missingness or data-quality data are reported.
MAJORLater sample-size amendment is incompletely documented.
The supplied protocol specifies 1,300 participants, while the trial subsequently planned to increase enrollment to 1,620 after unexpectedly high rates of SARS-CoV-2-negative participants, before stopping at 1,372.
MAJORTrial was substantially underpowered for the observed event rate.
The trial assumed a 20% placebo hospitalization rate but observed only 8.3%, and the study stopped before reaching the revised sample-size target.
MAJORRegistration and registry record inconsistencies.
ClinicalTrials.gov NCT04466540 (history) was first submitted 3 July 2020, about seven weeks after enrolment began on 12 May 2020, and the publication cites only this retrospective record. ClinicalTrials.gov records IPD sharing as 'No', contradicting the paper's statement that anonymised participant data can be made available on request. No results have been posted. The REBEC record still shows status 'Recruiting' with last enrolment 10 July 2020.
MAJORTreatment-initiation reporting shows unexplained arm-by-diagnostic-status asymmetry.
The results text states that 35 randomised patients never took study drug. The reported adherence percentages independently reproduce this exactly: 604/689 HCQ patients were fully adherent and 68/689 partially adherent, leaving 17 untreated; 583/683 placebo patients were fully adherent and 82/683 partially adherent, leaving 18 untreated. Figure 1, however, reports that within the mITT population 10 HCQ patients did not receive assigned treatment while all 471 placebo patients did.
MINORTable 1 nests comorbidities and symptoms under a treatments header.
The row 'Treatments at baseline 375/687 (54.6%)' heads a block that begins with azithromycin, ivermectin and oseltamivir but then continues without sub-headers into comorbidities (heart disease, lung disease, diabetes, hypertension, asthma) and then into presenting symptoms (fever, cough, sore throat, myalgia, fatigue, dyspnoea).
MINORIncorrect biologic-agent percentage.
Supplementary Table 3 reports biologic-agent use in the placebo arm as 5/683 = 0.07%, whereas the correct value is approximately 0.73%.
MINORInteger-granularity inconsistencies in Supplementary Table 2 percentages.
Numerous one-decimal percentages in the mITT baseline table cannot be generated by any integer event count using the stated arm denominators of 478 HCQ and 471 placebo. Most can be reconciled by modest variable-specific missingness, but those denominators are generally not reported.
MINORDuplicated value patterns in Table 1 worth verifying.
In the hydroxychloroquine arm only, the age split (329 / 360, 47.8% / 52.2%) is numerically identical to the sex split (329 / 360, 47.8% / 52.2%); the placebo arm shows no such coincidence. Respiratory rate is reported as 19.1 (2.5) with N=673 in BOTH arms - identical mean, SD and denominator - despite differing missingness on every other vital sign. Both as possible, but worth verifying.
MINORKaplan-Meier at-risk numbers imply zero censoring.
In Figure 2A the HCQ arm falls from 689 to 645 at day 30, a difference of exactly 44, the event count; placebo falls 683 to 626, exactly 57. Figure 2B behaves identically. This is consistent with the claim that no patients were lost to follow-up, however the eight consent withdrawals should have generated censoring events.
MINOREmbedded meta-analysis reported without PRISMA methods.
The meta-analysis in Figure 4 is presented with only a PROSPERO number (CRD42021265427), and no PRISMA flow diagram, search dates, eligibility criteria or risk-of-bias assessment. The 'evidence before this study' panel also refers to six prior RCTs evaluating hospitalisation while the forest plot contains five prior trials plus COPE.
MINORBMI categories are incomplete or mislabelled.
Table 1 defines the lowest BMI category as 'Normal (20-24.9)', followed by overweight (25-29.9) and obese (>=30), yet these three categories sum exactly to all 689 HCQ and all 683 placebo participants. The table therefore contains no category for BMI below 20.
|
risk of death, 0.7% lower, RR 0.99, p = 1.00, treatment 5 of 687 (0.7%), control 5 of 682 (0.7%), NNT 18741, all-cause death.
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risk of death, 56.0% higher, HR 1.56, p = 0.54, treatment 5 of 687 (0.7%), control 5 of 682 (0.7%), adjusted per study, univariate Firth's penalized likelihood.
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risk of mechanical ventilation, 32.4% higher, RR 1.32, p = 0.79, treatment 8 of 687 (1.2%), control 6 of 682 (0.9%).
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risk of ICU admission, 16.4% lower, RR 0.84, p = 0.61, treatment 16 of 687 (2.3%), control 19 of 682 (2.8%), NNT 219.
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risk of hospitalization, 23.5% lower, RR 0.77, p = 0.18, treatment 44 of 689 (6.4%), control 57 of 683 (8.3%), NNT 51.
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risk of hospitalization, 40.0% lower, RR 0.60, p = 0.15, treatment 267, control 255, <4 days.
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risk of hospitalization, 15.0% lower, RR 0.85, p = 0.49, treatment 422, control 428, ≥4 days.
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| Effect extraction follows pre-specified rules prioritizing more serious outcomes. Submit updates |
1.
Schwartz et al., Assessing the efficacy and safety of hydroxychloroquine as outpatient treatment of COVID-19: a randomized controlled trial, CMAJ Open, doi:10.9778/cmajo.20210069.
2.
Omrani et al., Randomized double-blinded placebo-controlled trial of hydroxychloroquine with or without azithromycin for virologic cure of non-severe Covid-19, eClinicalMedicine, doi:10.1016/j.eclinm.2020.100645.
Avezum et al., 31 Mar 2022, Double Blind Randomized Controlled Trial, Brazil, peer-reviewed, 40 authors, study period 12 May, 2020 - 7 July, 2021, average treatment delay 4.0 days, dosage 400mg bid day 1, 200mg bid days 2-7, trial NCT04466540 (history).
Hydroxychloroquine versus placebo in the treatment of non-hospitalised patients with COVID-19 (COPE – Coalition V): A double-blind, multicentre, randomised, controlled trial
The Lancet Regional Health - Americas, doi:10.1016/j.lana.2022.100243
Background Previous Randomised controlled trials (RCT) evaluating chloroquine and hydroxychloroquine in nonhospitalised COVID-19 patients have found no significant difference in hospitalisation rates. However, low statistical power precluded definitive answers.
Supplementary materials Supplementary material associated with this article can be found in the online version at doi:10.1016/j. lana.2022.100243.
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