Ivermectin for preventing and treating COVID‐19

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For outpatients, there is currently low‐ to high‐certainty evidence that ivermectin has no beneficial effect for people with COVID‐19. Based on the very low‐certainty evidence for inpatients, we are still uncertain whether ivermectin prevents death or clinical worsening or increases serious adverse events, while there is low‐certainty evidence that it has no beneficial effect regarding clinical improvement, viral clearance and adverse events. No evidence is available on ivermectin to prevent SARS‐CoV‐2 infection. In this update, certainty of evidence increased through higher quality trials including more participants. According to this review's living approach, we will continually update our search.

Ivermectin plus standard of care compared to standard of care plus/minus placebo probably has little or no effect on all‐cause mortality at day 28 (RR 0.77, 95% CI 0.47 to 1.25; 6 trials, 2860 participants; moderate‐certainty evidence) and little or no effect on quality of life, measured with the PROMIS Global‐10 scale (physical component mean difference (MD) 0.00, 95% CI ‐0.98 to 0.98; and mental component MD 0.00, 95% CI ‐1.08 to 1.08; 1358 participants; high‐certainty evidence). Ivermectin may have little or no effect on clinical worsening, assessed by admission to hospital or death within 28 days (RR 1.09, 95% CI 0.20 to 6.02; 2 trials, 590 participants; low‐certainty evidence); on clinical improvement, assessed by the number of participants with all initial symptoms resolved up to 14 days (RR 0.90, 95% CI 0.60 to 1.36; 2 trials, 478 participants; low‐certainty evidence); on serious adverse events (RR 2.27, 95% CI 0.62 to 8.31; 5 trials, 1502 participants; low‐certainty evidence); on any adverse events during the trial period (RR 1.24, 95% CI 0.87 to 1.76; 5 trials, 1502 participants; low‐certainty evidence); and on viral clearance at day 7 compared to placebo (RR 1.01, 95% CI 0.69 to 1.48; 2 trials, 331 participants; low‐certainty evidence). None of the trials reporting duration of symptoms were eligible for meta‐analysis.

We are uncertain whether ivermectin plus standard of care compared to standard of care plus/minus placebo reduces or increases all‐cause mortality at 28 days (risk ratio (RR) 0.60, 95% confidence interval (CI) 0.14 to 2.51; 3 trials, 230 participants; very low‐certainty evidence); or clinical worsening, assessed by participants with new need for invasive mechanical ventilation or death at day 28 (RR 0.82, 95% CI 0.33 to 2.04; 2 trials, 118 participants; very low‐certainty evidence); or serious adverse events during the trial period (RR 1.55, 95% CI 0.07 to 35.89; 2 trials, 197 participants; very low‐certainty evidence). Ivermectin plus standard of care compared to standard of care plus placebo may have little or no effect on clinical improvement, assessed by the number of participants discharged alive at day 28 (RR 1.03, 95% CI 0.78 to 1.35; 1 trial, 73 participants; low‐certainty evidence); on any adverse events during the trial period (RR 1.04, 95% CI 0.61 to 1.79; 3 trials, 228 participants; low‐certainty evidence); and on viral clearance at 7 days (RR 1.12, 95% CI 0.80 to 1.58; 3 trials, 231 participants; low‐certainty evidence). No trial investigated quality of life at any time point.

We identified 31 ongoing trials. In addition, there are 28 potentially eligible trials without publication of results, or with disparities in the reporting of the methods and results, held in ‘awaiting classification’ until the trial authors clarify questions upon request.

We excluded seven of the 14 trials included in the previous review version; six were not prospectively registered and one was non‐randomized. This updated review includes 11 trials with 3409 participants investigating ivermectin plus standard of care compared to standard of care plus/minus placebo. No trial investigated ivermectin for prevention of infection or compared ivermectin to an intervention with proven efficacy. Five trials treated participants with moderate COVID‐19 (inpatient settings); six treated mild COVID‐19 (outpatient settings). Eight trials were double‐blind and placebo‐controlled, and three were open‐label. We assessed around 50% of the trial results as low risk of bias.

We assessed RCTs for bias, using the Cochrane RoB 2 tool. We used GRADE to rate the certainty of evidence for outcomes in the following settings and populations: 1) to treat inpatients with moderate‐to‐severe COVID‐19, 2) to treat outpatients with mild COVID‐19 (outcomes: mortality, clinical worsening or improvement, (serious) adverse events, quality of life, and viral clearance), and 3) to prevent SARS‐CoV‐2 infection (outcomes: SARS‐CoV‐2 infection, development of COVID‐19 symptoms, admission to hospital, mortality, adverse events and quality of life).

We included randomized controlled trials (RCTs) comparing ivermectin to standard of care, placebo, or another proven intervention for treatment of people with confirmed COVID‐19 diagnosis, irrespective of disease severity or treatment setting, and for prevention of SARS‐CoV‐2 infection. Co‐interventions had to be the same in both study arms.

To assess the efficacy and safety of ivermectin plus standard of care compared to standard of care plus/minus placebo, or any other proven intervention for people with COVID‐19 receiving treatment as inpatients or outpatients, and for prevention of an infection with SARS‐CoV‐2 (postexposure prophylaxis).

Ivermectin, an antiparasitic agent, inhibits the replication of viruses in vitro. The molecular hypothesis of ivermectin's antiviral mode of action suggests an inhibitory effect on severe acute respiratory syndrome coronavirus 2 (SARS‐CoV‐2) replication in early stages of infection. Currently, evidence on ivermectin for prevention of SARS‐CoV‐2 infection and COVID‐19 treatment is conflicting.

Our confidence in the evidence, especially for outpatients, improved since the last review version, because we could look at more participants included in high‐quality trials. Although we are quite certain regarding our results on risk of people dying and quality of life, the confidence in the evidence is still low for many other outpatient and inpatient outcomes because there were only few events measured. The methods differed between trials, and they did not report everything we were interested in, such as relevant outcomes.

For treatment, there were five trials of people in hospital with moderate COVID‐19 and six trials of outpatients with mild COVID‐19. The trials used different doses of ivermectin and different durations of treatment.

We excluded seven of the 14 trials included in the previous review as these trials did not fulfil the expected ethical and scientific criteria. Together with four new trials, we included 11 trials with 3409 participants that investigated ivermectin combined with any usual care compared to the same usual care or placebo.

We wanted to update our knowledge of whether ivermectin reduces death, illness, and length of infection in people with COVID‐19, or is useful in prevention of the infection. We included trials comparing the medicine to placebo (dummy treatment), usual care, or treatments for COVID‐19 that are known to work to some extent, such as dexamethasone. We excluded trials comparing ivermectin to other medicines that do not work, like hydroxychloroquine, or whose effectiveness against COVID‐19 is uncertain.

Ivermectin is a medicine used to treat parasites, such as intestinal parasites in animals, and scabies in humans. It is inexpensive and is widely used in regions of the world where parasitic infestations are common. It has few unwanted effects.

This review aimed to provide a complete evidence profile, based on current Cochrane standards, for ivermectin with regard to efficacy and safety for postexposure prophylaxis of SARS‐CoV‐2 infection and treatment of COVID‐19. As this review ( Popp 2021b ), and the other reviews of the Cochrane Living Systematic Reviews Series on different interventions for COVID‐19 ( Ansems 2021 ; Kreuzberger 2021 ; Mikolajewska 2021 ; Popp 2021c ; Stroehlein 2021 ; Wagner 2021 ) are living systematic reviews during the COVID‐19 pandemic, specific adaptions related to the research question, including participants, interventions, comparators, outcomes, and methods were necessary for this update. We have transparently reported relevant protocol changes between the review and update in the section Differences between protocol and review .

As of January 2022, the efficacy and safety of ivermectin for COVID‐19 treatment and prophylaxis of SARS‐CoV‐2 infection are still subject to debate. The most recent guideline from the Association of Scientific Medical Societies in Germany (AWMF) stands by its recommendation against the use of ivermectin as antiviral treatment ( German AWMF Guideline 2021a ), while the Peruvian ministry of health removed its previous positive recommendation for the use of ivermectin entirely from its guideline ( The Guardian 2021b ). In February 2021, the US National Institutes of Health (NIH) revised its COVID‐19 treatment guidelines from a recommendation 'against the use of ivermectin' to 'cannot recommend either for or against the use of ivermectin,' giving clinicians leeway in individual case decision‐making ( NIH 2021 ). The WHO recommends the drug should only be used within clinical trials, as current evidence on the use of ivermectin to treat people with COVID‐19 is inconclusive ( WHO 2021b ).

Given the pace of the pandemic, it is important and welcome to make new scientific findings immediately available. But non‐peer‐reviewed results have to be handled with care and should not be used as the sole basis for clinical decisions and recommendations. Methodological limitations in the design of original trials, data integrity, and potential conflicts of interests have to be critically appraised when judging trial results. Many reviews and meta‐analyses of ivermectin for COVID‐19 are unreliable due to methodological inaccuracies and insufficient quality ( Popp 2021d ).

Several trials describe ivermectin's positive effect on resolution of mild COVID‐19 symptoms or describe a reduction of inflammatory marker levels or shorter time to viral clearance, while other trials indicate no effect or even a negative effect on disease progression. Many trials are already summarized in existing systematic reviews, meta‐analyses, and guidelines ( Bryant 2021a ; Izcovich 2021 ; NIH 2021 ). It should be kept in mind that several meta‐analyses and reviews have been retracted, or their updates show major methodologic inconsistencies ( Hill 2021b ; Kory 2021 ). Additionally, many of the original trials have been retracted or have not been published in peer‐reviewed journals, being only available on preprint servers without any supervising authority.

Ivermectin is an inexpensive and widely‐used medicine in humans and animals, mainly in low‐ and middle‐income countries with a high burden of parasitic diseases. The recently published in vitro studies, especially the results of Caly 2020 , have led to great interest in ivermectin in many countries with high numbers of SARS‐CoV‐2 infections, including the USA, countries of Central and South America and Asia. In South America in particular, people began liberally self‐medicating with ivermectin, and the drug has become part of public health policies without reliable scientific data; in May 2020, Bolivian health officials recommended ivermectin for the treatment of COVID‐19 without supplying evidence, and municipalities promoted the drug as a preventive measure ( Rodríguez‐Mega 2020 ). Due to growing interest in ivermectin and increasing hospitalizations for toxic side effects, the FDA discouraged the use of ivermectin to treat or prevent COVID‐19, and warned people not to self‐medicate with formulations intended for animals ( FDA 2020 ; Temple 2021 ).

Globally, the numbers of new COVID‐19 cases and deaths continue to increase with a substantial impact on healthcare systems. Vaccination remains a key response to address ongoing circulation and reduce the impact of emerging variants of concern. Despite efforts towards full vaccination uptake, pharmaceutical treatment interventions remain a mainstay in the management of COVID‐19. So far, the drug treatments shown to be effective against COVID‐19, and which are recommended in international guidelines, target SARS‐CoV‐2 itself or the immune response to the infection; for example dexamethasone, IL‐6 inhibitors, JAK‐inhibitors or monoclonal antibodies ( Ghosn 2021 ; Kreuzberger 2021 ; Wagner 2021 ; NIH 2021 ; WHO 2021b ).

The molecular hypothesis of ivermectin's antiviral mode of action, explained above, suggests an inhibitory effect on virus replication in the early stages of the disease, indicating a benefit especially for people with mild or moderate disease. This has also led to the idea of the possible preventive potency of ivermectin on infection with SARS‐CoV‐2 in individuals after exposure to a contagious contact, called postexposure prophylaxis. In response to the early promising in vitro studies on ivermectin, mentioned above, some COVID‐19 clinical trials were initiated to investigate the prophylactic and therapeutic effects of ivermectin.

Another member of the beta‐coronavirus family, SARS‐CoV‐1, which also causes respiratory failure, revealed similar dependence on the IMPα/β1 interaction ( Wulan 2015 ). The pathogen causing COVID‐19, SARS‐CoV‐2, is also a RNA virus closely related to SARS‐CoV‐1. In 2020, ivermectin gained much interest as a promising therapeutic option against SARS‐CoV‐2, when Caly 2020 published their experimental study results showing that ivermectin inhibits the replication of SARS‐CoV‐2 in cell culture. This observation has led to ivermectin being suggested as a potential antiviral agent that could prevent infection with SARS‐CoV‐2 completely or at least the progression to severe COVID‐19. However, until showing success in human clinical trials with patient‐relevant outcomes, these findings remain suggestive.

Before the COVID‐19 pandemic, only two clinical trials had been registered on ClinicalTrials.gov (clinicaltrials.gov/) using ivermectin as an intervention for treatment of viral diseases. Only one of these had published results ( Yamasmith 2018 ). In this small, single‐centre trial published as a conference abstract, ivermectin showed a shorter viral protein clearance time compared to placebo in people infected with dengue virus ( Yamasmith 2018 ).

One in vitro study showed that ivermectin can inhibit replication of HIV‐1, via inhibition of the interaction of virus proteins and a human cargo protein complex called importin (IMPα/β1) ( Wagstaff 2012 ). Importin is used by viruses for nuclear import in order to initiate their replication process ( Wagstaff 2012 ). Besides HIV‐1, various other RNA viruses use importin as target protein, among them dengue virus, West Nile virus, and influenza. Several research groups have investigated ivermectin's efficiency on those pathogens ( Goetz 2016 ; Tay 2013 ; Yang 2020 ). Although ivermectin showed some inhibitory potential for virus replication in vitro, there is no evidence of clinical effectiveness to date.

Adhering to recommended indications and doses, ivermectin is generally well tolerated. Adverse effects include weakness, drowsiness, diarrhoea, nausea, and vomiting. In addition, ivermectin can cause fever and rash ( González‐Canga 2008 ). Rare serious adverse effects can occur, such as vision problems, neurotoxicity, and liver damage. Those side effects seem to arise partially from ivermectin initiating the rapid death of parasites, especially when used for treatment of endoparasites, leading to hyperinflammation and anaphylactic reactions. Considering this pathomechanism, those effects should not occur in the treatment of viruses. However, the US Food and Drug Administration (FDA) has registered those toxic side effects in people using ivermectin in high doses for the treatment of COVID‐19 ( FDA 2020 ; González‐Canga 2008 ).

In animals and humans, ivermectin is easily absorbed by the mucosa if taken orally, or by the skin if used topically. As a lipophilic compound, it accumulates in fat and liver tissue from where it effuses and takes effect. Elimination is processed through bile and faeces ( Dourmishev 2005 ; González‐Canga 2008 ; Panahi 2015 ). Ivermectin is widely used in veterinary medicine, and is an essential drug for treating human parasitic diseases, such as onchocerciasis, lymphatic filariasis, strongyloidiasis, and scabies globally ( González‐Canga 2008 ). The established dosing regimen ranges from 150 µg/kg to 200 µg/kg administered orally, with a one‐ to two‐dose administration generally being effective. Dosing is generally low because of the agent's high potency ( Ashour 2019 ).

Ivermectin is an antiparasitic agent belonging to the group of avermectins, originally a fermentation metabolite produced by the bacterium Streptomyces avermitilis ( Campbell 1983 ). Ivermectin was introduced for medical use in 1982 and is effective against endoparasites such as Onchocerca volvulus and other helminths, as well as ectoparasites such as mites causing scabies and lice. The mode of action is based on binding to specific cell membrane channels that only occur in invertebrates ( Campbell 1983 ; Dourmishev 2005 ; Panahi 2015 ). Ivermectin is on the WHO List of Essential Medicines for its high effectiveness against human endoparasite and ectoparasite infestations ( WHO 2019 ).

Transmission is typically inferred from population‐level information. Inherent properties of virus variants of concern, and individual differences in infectiousness among individuals or groups make it difficult to contain its spread in the community ( WHO 2021a ). The global vaccination campaign progresses, with 11.8 billion doses administered by May 2022 ( Ritchie 2022 ), making a huge contribution in fighting the pandemic. However, global inequity ensures that not every region of the world has unlimited access to the vaccination. Therefore, the most effective, while ubiquitously available measures to control the virus spreading, are still non‐pharmaceutical interventions, including physical distancing, wearing a face mask (especially when distancing cannot be maintained), ventilating rooms, avoiding crowds and close contact, regularly cleaning hands, and coughing into a bent elbow or tissue ( WHO 2022b ). Research on prophylaxis of SARS‐CoV‐2 infection and treatment of COVID‐19 continues to be carried out globally. Evaluating the effectiveness of repurposed drugs represents one important strand of these research efforts. In this context, ivermectin — an antiparasitic intervention — has received substantial attention, especially in the Americas, parts of Asia, and Africa.

Data on mortality substantially differ between locations, depending on population characteristics, the case‐mix of infected and deceased individuals, other local factors, and changes during the ongoing outbreak. With > 70% in‐hospital mortality for people receiving ventilation ( Karagiannidis 2020 ), patients who survive often have considerable consequential damage ( Herrmann 2020 ; Prescott 2020 ). COVID‐19 can lead to death due to a variety of causes, such as severe respiratory failure, septic shock, and multiple organ failure ( WHO 2020a ). The worldwide case‐fatality ratio is estimated at 1.5%, with large statistical fluctuations (< 0.1% in Iceland up to almost 20% in Yemen; status January 2022) ( Dong 2020 ). However, these varying rates should not be interpreted as markers for the quality of health care ( Karagiannidis 2020 ), or the characteristics of different virus variants. Variations in case‐fatality ratios may be explained by the mean age of a population or of those infected, national vaccination rates, quality and extent of local testing strategies, and documentation and reporting systems ( Kobayashi 2020 ). The gold standard for confirming a SARS‐CoV‐2 infection is the reverse transcription‐polymerase chain reaction (RT‐PCR)‐based detection of viral ribonucleic acid (RNA) from a nasopharyngeal swab test, sputum, or tracheal secretion, with sensitivity ranging from 70% to 98%, depending on pretest probability ( Watson 2020 ). Offering lower sensitivity but greater practicality and accessibility, antigen tests are the primary instrument for COVID‐19 diagnosis, especially in point‐of‐care testing ( WHO 2020b ).

Available data suggest that one‐third of SARS‐CoV‐2 infections remain asymptomatic ( Oran 2021 ), but there is still uncertainty around this estimate. About 80% of symptomatic cases show mild symptoms, including cough, fever, myalgia, headache, dyspnoea, sore throat, diarrhoea, nausea and vomiting, and loss of smell and taste. Outpatient management is appropriate for most people with a mild course of COVID‐19. Moderate, severe, and critical cases (approximately 20%), with the need for oxygen supplementation, ventilatory support, or intensive medical care, cause a considerable burden for healthcare systems. Defined risk factors for severe disease include increasing age (over 60 years) and certain comorbidities ( Huang 2020 ; WHO 2020a ). Comorbidities such as cardiovascular disease, diabetes mellitus, chronic obstructive pulmonary disease and other lung diseases, malignancies, chronic kidney disease, solid organ or haematopoietic stem cell transplantation, and obesity are associated with severe COVID‐19 and mortality ( Deng 2020 ; Williamson 2020 ).

To assess the efficacy and safety of ivermectin plus standard of care compared to standard of care plus/minus placebo, or any other proven intervention for people with COVID‐19 receiving treatment as inpatients or outpatients, and for prevention of an infection with SARS‐CoV‐2 (postexposure prophylaxis).

In case of emerging policy relevance due to global controversies around the intervention, we will consider republishing an updated review even though our conclusions remain unchanged. We will review the scope and methods of the review approximately monthly, or more frequently if appropriate, in light of potential changes in COVID‐19 research (e.g. when additional comparisons, interventions, subgroups, or outcomes, or new review methods become available).

We will wait until the accumulating evidence changes our conclusions of the implications for research and practice before republishing the review. We will consider one or more of the following components to inform this decision.

Our information specialist (MIM) provided us with a weekly monitoring of published RCTs up to and including February 2022. From April onwards we will change this list to a monthly monitoring schedule, which two review authors will screen, extract, evaluate, and integrate following the guidance for Cochrane living systematic reviews ( Cochrane LSR ).

Very low certainty: we have very little confidence in the effect estimate; the true effect is likely to be substantially different from the estimate of effect.

Moderate certainty: we are moderately confident in the effect estimate; the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different.

We had planned to create separate summary of findings tables for the use of ivermectin with different intentions (e.g. treatment of people with COVID‐19 in inpatient and outpatient settings, and prevention of SARS‐CoV‐2 infection) and for different comparisons with regard to the intervention and comparator. For the current review, we found no trials with active comparators. The summary of findings tables included the following outcomes.

Two review authors (SW, MP) assessed the certainty of evidence, considering risk of bias, inconsistency, imprecision, indirectness, and publication bias. We used the overall RoB 2 assessment and RoB sensitivity analysis to inform the risk of bias judgement underlying the assessment of the certainty of evidence.

We presented the main results of the review in summary of findings tables, including a rating of the certainty of evidence based on the GRADE approach. We followed current GRADE guidance as recommended in the Cochrane Handbook for Systematic Reviews of Interventions ( Schünemann 2020 ).

trials reporting data as median instead of mean for continuous outcomes; in the current review version there were no data reported as median that were eligible for a transformation into mean;

We reported details of the intervention and severity of the condition at baseline for each trial in the footnotes of the forest plot. We investigated heterogeneity by visual inspection of the forest plot. We planned to investigate heterogeneity by subgroup analysis to calculate RR or MD in conjunction with the corresponding CI for each subgroup, if sufficient trials had been available (at least 10 trials per outcome); the current review had insufficient trials. In review updates, we will perform subgroup analyses if statistical heterogeneity is present (P < 0.1 for the Chi 2 test of heterogeneity, I 2 ≥ 50%, or a different clinical conclusion of 95% CI versus 95% PI).

We planned to present descriptive statistics only if we deemed meta‐analysis inappropriate for a certain outcome because of heterogeneity or because of serious trial limitations leading to considerably high risk of bias (e.g competing risk of death not taken into account in outcome measurement). This was not the case for the current review version.

If clinical and methodological characteristics of individual trials were sufficiently homogeneous, we pooled the data in meta‐analyses. When meta‐analysis was feasible, we used the random‐effects model as we assumed that the intervention effects were related but were not the same for the included trials. For dichotomous outcomes, we performed meta‐analyses using the Mantel‐Haenszel method under a random‐effects model to calculate the summary (combined) intervention effect estimate as a weighted mean of the intervention effects estimated in the individual trials. For continuous outcomes, we used the inverse‐variance method.

In the previous review version, we excluded high risk of bias trials from the primary analysis, with the aim to eliminate biased data and untrustworthy trials. However, to be transparent, we presented all trials in a secondary analysis. With the introduction of our new research integrity assessment, differentiation between primary and secondary analyses based on RoB ratings became dispensable. All included trials were eligible for the main analyses which informed the summary of findings tables and concerns regarding risk of bias were met with respective sensitivity analysis (see Sensitivity analysis ).

When there are 10 or more relevant trials pooled in a meta‐analysis, we planned to investigate risk of reporting bias (publication bias) in pairwise meta‐analyses using contour‐enhanced funnel plots. In the current review, there were no meta‐analyses including 10 or more trials. For review updates, if funnel plot asymmetry is suggested by a visual assessment, we plan to perform exploratory analyses (e.g. Rücker's arcsine test for dichotomous data and Egger's linear regression test for continuous data) to further investigate funnel plot asymmetry. We will consider P < 0.1 as the level of statistical significance. In review updates, we will analyse reporting bias using the open‐source statistical software R package meta ( Meta ).

We sought to identify all research that met our predefined eligibility criteria. Missing trials can introduce bias to the analysis. We searched for completed non‐published trials in trials registers, contacted authors to seek assurance that the results will be made available, and classified them as 'awaiting classification' until the results are reported. We reported the number of completed non‐published trials.

We measured statistical heterogeneity using the Chi 2 test and the I 2 statistic ( Deeks 2020 ), and the 95% prediction interval (PI) for random‐effects meta‐analysis ( IntHout 2016 ). The prediction interval helps in the clinical interpretation of heterogeneity by estimating what true treatment effects can be expected in future settings ( IntHout 2016 ). We restricted calculation of a 95% PI to meta‐analyses with four or more trials (200 participants or more), since the interval would be imprecise when a summary estimate was based on only a few small trials. We used the open‐source statistical software R package meta to calculate 95% PIs ( Meta ). We declared statistical heterogeneity if P < 0.1 for the Chi 2 statistic, or I 2 statistic ≥ 40% (40% to 60%: moderate heterogeneity; 50% to 90%: substantial heterogeneity; 75% to 100%: considerable heterogeneity; Deeks 2020 ), or the range of the 95% PI revealed a different clinical interpretation of the effect estimate compared to the 95% CI.

We used the descriptive statistics reported in the Characteristics of included studies table to assess whether the trials within each pairwise comparison were homogeneous enough, with respect to trial and intervention details and population baseline characteristics, that the assumption of homogeneity might be plausible. In case of excessive clinical heterogeneity, we did not pool the findings of included trials.

We have taken into account a number of potential sources of missing data in a systematic review or meta‐analysis, which can affect the number of trials, outcomes, summary data, individuals, or study‐level characteristics ( Deeks 2020 ). Incomplete data can introduce bias into the meta‐analysis, if they are not missing at random. Missing trials may be the result of reporting bias, and we addressed this as described in the Assessment of reporting biases section. Missing outcomes and summary data may be the result of selective reporting bias; missing individuals may be the result of attrition from the trial or lack of intention‐to‐treat analysis. We addressed these sources of missing data using the RoB 2 tool ( Assessment of risk of bias in included studies ). If data were incompletely reported, we contacted the trial authors to request additional information.

In trials with multiple intervention groups, we combined groups if reasonable (e.g. trial arms with different doses of ivermectin). If it had not been reasonable to pool the groups, we planned to split the 'shared' comparator group to avoid double‐counting participants. There was no need to split shared groups for the current review.

We considered effect estimates of dichotomous outcomes with the range of the 95% CIs not crossing 1 and continuous outcomes with the range of the 95% CIs not crossing 0 as statistically significant effect estimates. A statistically significant effect does not necessarily mean that the estimated effect is clinically relevant. We assessed the clinical relevance of the effect size separately and reported it transparently.

If available for future review updates, we plan to extract and report hazard ratios (HRs) for time‐to‐event outcomes (e.g. time to death). If HRs are not available, we will make every effort to estimate the HR as accurately as possible from available data using the methods proposed by Parmar 1998 and Tierney 2007 . If sufficient trials had provided HRs, we planned to use HRs rather than RRs or MDs in a meta‐analysis, as they provide more information.

For continuous outcomes, we recorded the mean, standard deviation (SD), and the number of analysed participants in the intervention and control groups. If the SD was not reported, we used standard errors, CIs, or P values to calculate the SD with the formulas described in the Cochrane Handbook for Systematic Reviews of Interventions ( Higgins 2020d ). If trials reported data as median with interquartile range (IQR), we assumed that the median was similar to the mean when sample sizes were large and the distribution of the outcome was similar to the normal distribution. In these cases, the width of the interquartile range (IQR) is approximately 1.35 SDs ( Higgins 2020d ). We used the MD with 95% CI as effect measure.

Similarly, we reached an overall risk of bias judgement for a specific outcome by considering all domains resulting in one of the three judgement options described above. Overall low risk of bias of the trial result was assumed when all domains were at low risk; some concerns of bias was assumed when the trial result was judged to raise some concerns in at least one domain for this result, but not at high risk of bias for any domain; overall high risk of bias of the trial result was assumed when the trial was at high risk of bias in at least one domain for this result or when it was judged to have some concerns for multiple domains in a way that substantially lowered confidence in the result ( Higgins 2020c ).

We assessed risk of bias in the included trials using the Cochrane RoB 2 tool ( Higgins 2020c ; Sterne 2019 ). The effect of interest was the effect of assignment at baseline, regardless of whether the interventions were received as intended (the 'intention‐to‐treat effect'). We assessed the risk of bias for all results (outcomes) reported in the included trials that we specified as outcomes for the current review and that contributed to the review's summary of findings tables.

Five review authors in teams of two (MP, SR, SS, RH, SW), independently extracted data using a standardized data extraction form, including details of the trial, participants, intervention, comparator, and outcomes. If necessary, we tried to obtain missing data by contacting the authors of relevant articles. At each step of data extraction, we resolved any discrepancies through discussion between the review authors.

During this pandemic, several trials investigating ivermectin for COVID‐19 turned out to be problematic and were either retracted or concerns were expressed due to misconduct or lack of research integrity ( BBC NEWS ; Elgazzar 2020 ; Retraction Watch Database (ivermectin) ; Samaha 2021 ). A ‘problematic study’ is defined by Cochrane as "Any published or unpublished study where there are serious questions about the trustworthiness of the data or findings, regardless of whether the study has been formally retracted; scientific misconduct will not be the only reason that a study might be problematic; problems may result from poor research practices or honest errors" ( Cochrane policy ‐ managing problematic studies ). To respond to these facts and developments, we changed the inclusion criteria for this review update to identify and handle problematic trials, and considered research integrity of the individual trial as an important eligibility criteria. Current standard tools for systematic reviews do not systematically consider issues of research integrity. However, there are useful tools available, such as the REAPPRAISED checklist for evaluation of publication integrity ( Grey 2020 ), or the data extraction sheet from Cochrane Pregnancy and Childbirth that addresses scientific integrity and trustworthiness ( Data extraction template ). Additionally, there is available implementation guidance on the Cochrane policy of managing potentially problematic studies ( Implementation guidance ‐ problematic studies ). We used the Cochrane implementation guidance, modified the existing tools and developed a specific tool for the current review. This tool along with detailed methodological instructions and critical and important signalling questions to key aspects (domains), is available in Appendix 2 and described elsewhere ( Weibel 2022 ). Briefly, trials were only eligible for the current review update if they met critical aspects assuring research integrity, such as retraction notices, prospective trial registration, ethics approval, plausible study authorship, sufficient reporting of methods regarding relevant eligibility criteria (e.g. randomization), and plausibility of study results. Two review authors independently re‐evaluated all trials included in the original review version and assessed all new and eligible trials for research integrity. We excluded trials if they were retracted or if they were not prospectively registered in a national or international trials' registry according to the WHO guidelines for clinical trial registration ( WHO 2018 ). We held all potentially eligible trials with disparities between the reporting of methods and results in ‘awaiting classification’ until the trial authors can clarify certain questions upon request. We documented the process and transparently reported all decisions.

We documented the trial selection process in a PRISMA flow diagram with the total number of trials included, excluded, awaiting classification, and ongoing ( Moher 2009 ). We listed the reasons for exclusion and awaiting classification in the Characteristics of excluded studies and Characteristics of studies awaiting classification tables.

We performed trial selection in accordance with the Cochrane Handbook for Systematic Reviews of Interventions ( Lefebvre 2020 ). Two out of three review authors (MP, SR, SW) independently screened titles and abstracts of identified records. We retrieved full‐text articles and independently assessed eligibility of the remaining records against the predefined eligibility criteria. We resolved discrepancies through discussion between the review authors. We included trials irrespective of whether measured outcome data were reported in a 'usable' way. We collated multiple reports of the same trial, so that the trial, rather than the report, was the unit of interest in the review.

Since the date of last search (16 December 2021) up to and including February 2022, we used the CCSR to monitor newly published results of RCTs on ivermectin on a weekly basis. In February 2022 we closed the trial pool for this review update. From April onwards we changed our screening to a monthly monitoring schedule, which two review authors will screen. In April, we identified one trial including > 1000 participants. We included this single trial due to its large size and considered this a justifiable compromise between being as up to date as possible in the dynamic of this pandemic and reasons of practicability.

We reported time points of outcome measurement in the footnotes of the forest plots. We included serious adverse events and adverse events occurring during the trial period, including adverse events during active treatment and long‐term adverse events as well. If sufficient data are available for review updates, we will group the measurement time points of eligible outcomes into those measured directly after treatment (up to 7 days), medium‐term outcomes (up to 14 days), and longer‐term outcomes (28 days or more).

We collected information on outcomes from all time points reported in the publications. If only a few trials contributed data to an outcome, we pooled different time points, provided the trials had produced valid data and pooling was clinically reasonable.

Development of clinical COVID‐19 symptoms up to 14 days; assessed in accordance with individual items of the WHO scale ( Marshall 2020 ). If the trial did not use a standardized scale to assess the status of the participants, we categorized their status according to the WHO scale with the information provided by the trial:

We analysed different outcomes for the use of ivermectin for treatment of people with COVID‐19 in inpatient and outpatient settings, and for the prevention of SARS‐CoV‐2 infection. If trials were eligible for inclusion regarding design, population, intervention, and comparator, but did not report outcomes of interest, they were not included for meta‐analysis. However, we summarized reported outcomes for all included trials in the Characteristics of included studies table.

We evaluated core outcomes in accordance with the Core Outcome Measures in Effectiveness Trials (COMET) Initiative for COVID‐19 patients ( COMET 2020 ; Marshall 2020 ), and additional outcomes that have been prioritized by consumer representatives and the German guideline panel for inpatient therapy of people with COVID‐19 ( German AWMF Guideline 2021a ) and for outpatient therapy ( German AWMF Guideline 2021b ). The current outcome set differed between previous protocols and reviews and the current review. Changes to the outcomes were necessary due to the risk of competing events associated with the original outcome set. We added outcomes for inpatients and outpatients that aim to simultaneously capture all participants of the population with clinical worsening and all participants with clinical improvement. This was possible by using composite outcomes, e.g. combining new need for invasive mechanical ventilation and death as clinical worsening for inpatients, and combining admission to hospital and death for outpatients. This adjusted outcome set should allow evidence on ivermectin to become more unambiguous and patient‐relevant.

Trials investigating various concomitant medications (e.g. doxycycline, hydroxychloroquine, azithromycin, zinc) in addition to ivermectin or as comparator drug were not eligible for this review. Due to unproven efficacy, possible adverse effects, and drug interactions, these comparisons may confound the assessment of the efficacy or safety of ivermectin.

We planned to compare ivermectin to any other active pharmacological comparator with proven efficacy for prevention or treatment of COVID‐19. Proven interventions were defined as those recommended by the WHO living guideline ( Agarwal 2020 ). As of 8 December 2021, strong recommendations for dexamethasone and for IL‐6 receptor blockers (tocilizumab and sarilumab) in critically ill COVID‐19 patients, and conditional recommendations for casirivimab and imdevimab for COVID‐19 patients with high risk of severe disease and for critically‐ill patients with seronegative status were available ( Agarwal 2020 ). For patients that qualify for a proven active intervention, it would be unethical to further conduct trials that use placebo only. In contrast, trials using comparators (e.g. azithromycin, Popp 2021c ) with proven ineffectiveness may confound the assessment of the efficacy or safety of ivermectin, and therefore we excluded such trials. Although those types of interventions were possibly used at a certain point of time during the pandemic with the best intentions, their use was never supported by actual evidence, and they have potential adverse effects ( Popp 2021c ; Singh 2021 ). From those comparisons, no reliable evidence can be obtained.

We considered all doses and regimens of ivermectin eligible and pooled them for the analysis. We considered and categorized dosing schemes into low (≤ 0.2 mg/kg orally, single dose) and high doses (> 0.2 mg/kg orally, single dose or with higher frequency). We plan to analyse different doses in subgroup analyses, if sufficient trials are available for review updates.

We included trials investigating participants who were not infected with SARS‐CoV‐2 at enrolment, but were at high risk of developing the infection (e.g. after high‐risk exposure), regardless of age, gender, ethnicity, disease severity, and setting (inpatient and outpatients). Participants may have been hospitalized for reasons other than COVID‐19. Eligible trials must have reported the history of previous SARS‐CoV‐2 infections or serological evidence and the vaccination status in included participants. A history of SARS‐CoV‐2 infection or vaccination was not an exclusion criterion.

We included trials investigating participants with confirmed SARS‐CoV‐2 infection (RT‐PCR or antigen testing), regardless of age, gender, ethnicity, disease severity, and setting (inpatients and outpatients). If trials included participants with a confirmed or suspected COVID‐19 diagnosis, we used only the data for the patient population with confirmed COVID‐19 diagnosis. In cases, where data were not reported separately for people with confirmed or suspected COVID‐19 diagnosis, we excluded the trial.

We included full‐text journal articles published in PubMed‐indexed and non‐indexed journals, preprint articles, results published in trials registers, and abstract publications. We applied no restrictions on the language of publication of the articles. All trials, especially preprint articles that have not been peer‐reviewed, must have reported robust and valid data on trial design, participants' characteristics, interventions, and outcomes, to be eligible for inclusion.

We included randomized controlled trials (RCTs) only, as this is the best trial design for evaluating the efficacy of interventions ( Higgins 2020a ). Non‐standard RCT designs, such as cluster‐randomized and cross‐over trials, were not eligible for the review ( Higgins 2020b ). These designs are not appropriate in this context, since the underlying cause of COVID‐19 is an infection with the SARS‐CoV‐2 virus and the medical condition evolves over time.

Two trials comparing ivermectin plus standard of care to standard of care plus placebo reported data on viral clearance at day 14 for 588 participants with mild disease ( Bounfrate 2021 ; Vallejos 2021 ). In the ivermectin group 243 participants and in the comparator group 237 participants reached viral clearance at day 14 ( ). Ivermectin plus standard of care showed no effect compared to standard of care plus placebo for viral clearance at day 14 (RR 0.96, 95% CI 0.90 to 1.03; 2 trials, 588 participants). Both trials had low risk of bias, were peer‐reviewed, and started treatment early.

Two trials comparing ivermectin plus standard of care to standard of care plus placebo reported viral clearance at day 7 in 331 participants with mild disease ( Chaccour 2021 ; TOGETHER 2022 ). Thirty‐seven participants in the ivermectin group and 42 participants in the placebo group reached viral clearance at day 7 ( ). Ivermectin plus standard of care may have little or no effect on viral clearance at day 7 compared to placebo (RR 1.01, 95% CI 0.69 to 1.48; 2 trials, 331 participants; low‐certainty evidence). We downgraded the certainty of evidence one level for serious risk of bias and one level for serious imprecision due to a wide CI. One trial had some concerns regarding risk of bias ( TOGETHER 2022 ). The sensitivity analysis, including only one trial with low risk of bias estimated the intervention effect with more imprecision at RR 3.00 (95% CI 0.13 to 67.06; 1 trial, 24 participants), supporting the decision on the certainty of the evidence. Both trials were published as a journal article and started treatment early.

Two trials comparing ivermectin plus standard of care to standard of care plus placebo reported data on viral clearance at day 3 in 819 participants with mild disease ( Vallejos 2021 ; TOGETHER 2022 ). In the ivermectin group 124 participants and in the comparator group 137 participants reached viral clearance at day 3 ( ). Ivermectin plus standard of care showed no effect compared to standard of care plus placebo for viral clearance at day 3 (RR 0.93, 95% CI 0.78 to 1.12; 2 trials, 819 participants). Sensitivity analysis excluding one trial with some concerns regarding risk of bias ( TOGETHER 2022 ), did not change the conclusion (RR 0.95, 95% CI 0.78 to 1.14; 1 trial, 501 participants). Both trials started treatment early and were peer‐reviewed.

TOGETHER 2022 reported this outcome as adverse events separated into grade 1 to 4 for outpatients at 28 day which was not eligible for meta‐analysis of adverse events of any grade, since one patient could experience several outcomes of different grades and would therefore potentially be counted multiple times.

Five trials comparing ivermectin plus standard of care to standard of care plus/minus placebo reported data for any adverse events during the trial period for 1502 participants with mild disease ( Bounfrate 2021 ; Chaccour 2021 ; I‐TECH 2022 ; López‐Medina 2021 ; Vallejos 2021 ). In the ivermectin group 280 participants and in the comparator group 237 participants experienced adverse events during the trial period ( ). Ivermectin plus standard of care may have little or no effect on any adverse events during the trial period compared to standard of care plus/minus placebo (RR 1.24, 95% CI 0.87 to 1.76; 5 trials, 1502 participants; low‐certainty evidence). We downgraded the certainty of evidence one level for serious risk of bias. We did not downgrade two levels for risk of bias because exclusion of one unblinded trial with high risk of bias revealed an effect estimate of RR 1.07 (0.84 to 1.36), indicating no difference between ivermectin and placebo. We downgraded the certainty of evidence another level for serious inconsistency due to substantial heterogeneity between trials (I 2 = 80%, 95% PI 0.38 to 4.02). Sensitivity analysis only including trials with low risk of bias ( Chaccour 2021 ; Vallejos 2021 ), estimated the effect of the intervention at RR 0.94 (95% CI 0.65 to 1.37; 2 trials, 525 participants) which did not change the conclusion. All trials started treatment no longer than an average of 5 days after symptom onset.

Five trials comparing ivermectin plus standard of care to standard of care plus/minus placebo reported data on serious adverse events during the trial period for 1502 participants with mild disease ( Bounfrate 2021 ; Chaccour 2021 ; I‐TECH 2022 ; López‐Medina 2021 ; Vallejos 2021 ). With 13 participants experiencing serious adverse events, there were very few events overall ( ). Ivermectin plus standard of care may have little or no effect on serious adverse events during the trial period compared to standard of care plus/minus placebo (RR 2.27, 95% CI 0.62 to 8.31; 5 trials, 1502 participants; low‐certainty evidence). Heterogeneity was low (I 2 = 0) and the 95% PI was not presented because it was not reliable as two out of five trials were not estimable due to zero events in both trial arms. We downgraded the certainty of evidence one level for serious risk of bias and one level for serious imprecision due to very few events and a wide CI. Sensitivity analysis only including trials with low risk of bias ( Vallejos 2021 ), revealed a non‐estimable effect of the intervention due to zero events (1 trial, 501 participants). All trials started treatment no longer than an average of 5 days after symptom onset.

For the mental component, the mean score in participants in the ivermectin group was 52.5 points with a SD of 11.2 points and 52.5 points with a SD of 9 points in the comparator group ( ). Ivermectin plus standard of care has little or no effect on quality of life at up to 28 days compared to standard of care plus placebo (MD 0.00, 95% CI ‐1.08 to 1.08; 1 trial, 1358 participants; high‐certainty evidence).

The trial reported data as median with IQR, and we transformed the data into mean with standard deviation (SD). For the physical component, the mean score in participants in the ivermectin group was 49.6 points with a SD of 7.8 points and 49.6 points with a SD of 10.4 points in the comparator group ( ). Ivermectin plus standard of care has little or no effect on quality of life at up to 28 days compared to standard of care plus placebo (mean difference (MD) 0.00, 95% CI ‐0.98 to 0.98; 1 trial, 1358 participants; high‐certainty evidence).

One trial comparing ivermectin plus standard of care to standard of care plus placebo reported quality of life at up to 28 days in 1458 participants with mild disease ( TOGETHER 2022 ). In the trial, health‐related quality of life was measured on a standardized scale using the PROMIS Global‐10 scale, separated into a physical and mental component. Normalized scores from 16.2 and 21.2 points to 67.7 and 67.6 points, indicate lowest to the highest physical and mental quality of life, respectively.

Two trials comparing ivermectin plus standard of care to standard of care plus placebo reported data on time of symptom resolution ( López‐Medina 2021 ; TOGETHER 2022 ). In both trials, data were reported as median with interquartile range (IQR) in 398 and 1358 participants with mild disease, respectively. In López‐Medina 2021 the median duration of symptom resolution in the ivermectin group was 10 days (IQR 9 to 13 days) compared to 12 days (IQR 9 to 13 days) in the placebo group; TOGETHER 2022 reported 14 days (IQR 11 to 14 days) for both groups. Neither trial was eligible for meta‐analysis due to asymmetric distribution of the data. Bounfrate 2021 narratively reported median time to symptom resolution but without IQRs.

Two trials comparing ivermectin plus standard of care to standard of care plus placebo reported data on symptom resolution at 28 days in 478 participants with mild disease ( Bounfrate 2021 ; López‐Medina 2021 ). In the ivermectin group 204 participants and in the comparator group 177 participants were asymptomatic at day 28 ( ). Ivermectin plus standard of care showed no effect compared to standard of care plus placebo for improvement of clinical status, assessed by the number of participants with all initial symptoms resolved up to 28 days (RR 1.03, 95% CI 0.94 to 1.13; 2 trials, 478 participants). Sensitivity analysis excluding the trial with some concerns regarding risk of bias widened the CI, but did not change the conclusion (RR 0.97, 95% CI 0.75 to 1.25; 1 trial, 80 participants). Both trials started treatment early and were peer‐reviewed.

Two trials comparing ivermectin plus standard of care to standard of care plus placebo reported data on symptom resolution at 14 days in 478 participants with mild disease ( Bounfrate 2021 ; López‐Medina 2021 ). In the ivermectin group 143 participants and in the comparator group 133 participants were asymptomatic at day 14 ( ). Ivermectin plus standard of care may have little or no effect compared to standard of care plus placebo on clinical improvement, assessed by the number of participants with all initial symptoms resolved up to 14 days (RR 0.90, 95% CI 0.60 to 1.36; 2 trials, 478 participants; low‐certainty evidence). We downgraded one level for serious risk of bias and one level for serious inconsistency, due to substantial heterogeneity between trials (I 2 = 57%). Sensitivity analysis excluding the trial with some concerns regarding risk of bias widened the CI, but did not change the conclusion (RR 0.67, 95% CI 0.38 to 1.16; 1 trial, 80 participants). Both trials started treatment early and were peer‐reviewed.

One trial comparing ivermectin plus standard of care to standard of care alone reported data on clinical worsening, assessed by need for ICU admission or death within 28 days for 490 participants with mild disease ( I‐TECH 2022 ). Eight participants in the ivermectin group and 13 participants in the comparator group showed clinical worsening ( ). Due to a very wide CI and few events, the effect of ivermectin plus standard of care compared to standard of care alone for ICU admission or death within 28 days remained unclear (RR 0.64, 95% CI 0.27 to 1.51; 1 trial, 490 participants). The trial had low risk of bias, started treatment early, and was peer‐reviewed.

Two trials comparing ivermectin plus standard of care to standard of care plus placebo reported data on clinical worsening, assessed by admission to hospital or death within 28 days for 590 participants with mild disease ( Bounfrate 2021 ; Vallejos 2021 ). Eighteen participants in the ivermectin group and 21 participants in the comparator group showed clinical worsening ( ). Ivermectin plus standard of care may have little or no effect compared to standard of care plus placebo on clinical worsening, assessed by admission to hospital or death within 28 days (RR 1.09, 95% CI 0.20 to 6.02; 2 trials, 590 participants; low‐certainty evidence). We downgraded the certainty of evidence one level for serious inconsistency, due to moderate heterogeneity between trials (I 2 = 44%) and one level for serious imprecision due to few events and a wide CI. Both trials had low risk of bias, were peer‐reviewed, and started treatment early.

Six trials comparing ivermectin plus standard of care to standard of care plus/minus placebo reported data on mortality at day 28 for 2860 participants with mild disease ( Bounfrate 2021 ; Chaccour 2021 ; I‐TECH 2022 ; López‐Medina 2021 ; TOGETHER 2022 ; Vallejos 2021 ). Sixty‐six deaths occurred overall, 28 in the ivermectin group and 38 in the comparator group ( ). Ivermectin plus standard of care probably has little or no effect compared to standard of care plus/minus placebo on all‐cause mortality at day 28 (RR 0.77, 95% CI 0.47 to 1.25; 6 trials, 2860 participants; moderate‐certainty evidence). Heterogeneity was low (I 2 = 0) and the 95% prediction interval (PI) (0.26 to 2.25) revealed a similar clinical interpretation of the effect estimate compared to the 95% CI. We downgraded the certainty of evidence one level for serious imprecision due a wide CI. Sensitivity analysis, excluding one trial with some concerns regarding risk of bias ( López‐Medina 2021 ), did not change the conclusion (RR 0.75, 95% CI 0.38 to 1.46; 5 trials, 2462 participants). All trials started treatment no longer than an average of 5 days after symptom onset.

Three trials comparing ivermectin plus standard of care to standard of care plus/minus placebo reported viral clearance at day 7 in 231 participants with moderate disease ( Kirti 2021 ; Mohan 2021 ; Pott‐Junior 2021 ). Sixty‐three participants in the ivermectin group and 34 participants in the comparator group reached viral clearance at day 7 ( ). Ivermectin plus standard of care may have little or no effect on viral clearance at 7 days compared to standard of care plus/minus placebo (RR 1.12, 95% CI 0.80 to 1.58; 3 trials, 231 participants; low‐certainty evidence). We downgraded the certainty of evidence one level for serious risk of bias and one level for serious imprecision due to few participants and a wide CI. Excluding two trials with high risk of bias regarding this outcome ( Kirti 2021 ; Pott‐Junior 2021 ) did not change the conclusion (RR 1.33, 95% CI 0.80 to 2.20; 1 trial, 125 participants). This sensitivity analysis is the same as for analysing the only trial that started treatment early ( Mohan 2021 ). All trials were published as journal articles.

One trial comparing ivermectin plus standard of care to standard of care plus placebo reported viral clearance at day 3 in 125 participants with moderate disease ( Mohan 2021 ). Ten participants in the ivermectin group and 7 participants in the placebo group reached viral clearance at day 7 ( ). Due to a very wide CI and few participants, the effect of ivermectin plus standard of care compared to standard of care plus placebo for viral clearance at day 3 remained unclear (RR 0.80, 95% CI 0.33 to 1.96; 1 trial, 125 participants). The trial had low risk of bias, was published in a journal, and started treatment early.

Three trials comparing ivermectin plus standard of care to standard of care plus/minus placebo reported any adverse events during the trial period in 228 participants with moderate disease ( Krolewiecki 2021 ; Mohan 2021 ; Pott‐Junior 2021 ). Thirty‐four participants in the ivermectin group and 13 participants in the comparator group experienced adverse events ( ). Ivermectin plus standard of care may have little or no effect on any adverse events during the trial period compared to standard of care plus/minus placebo (RR 1.04, 95% CI 0.61 to 1.79; 3 trials, 228 participants; low‐certainty evidence). We downgraded the certainty of evidence one level for serious risk of bias and one level for serious imprecision due to few participants and a wide CI. We did not judge any trial at low risk of bias, and sensitivity analysis excluding two trials with high risk of bias regarding this outcome ( Krolewiecki 2021 ; Pott‐Junior 2021 ), did not change the conclusion (RR 1.21, 95% CI 0.50 to 2.97; 1 trial, 152 participants). The same accounts for excluding the trial that started treatment late after symptom onset ( Pott‐Junior 2021 ), which resulted in an estimated effect of the intervention at RR 1.26 (95% CI 0.69 to 2.31; 2 trials, 197 participants). All trials were published as journal articles.

Two trials comparing ivermectin plus standard of care to standard of care plus/minus placebo reported serious adverse events during the trial period in 197 participants with moderate disease ( Krolewiecki 2021 ; Mohan 2021 ). Only one participant showed any serious adverse events in the ivermectin group ( ). We are uncertain whether ivermectin plus standard of care increases or reduces serious adverse events during the trial period compared to standard of care plus/minus placebo (RR 1.55, 95% CI 0.07 to 35.89; 2 trials, 197 participants; very low‐certainty evidence). We downgraded the certainty of evidence one level for serious risk of bias and two levels for very serious imprecision due to few participants, very few events, and wide CI. Sensitivity analysis was not necessary since both trials had some concerns regarding risk of bias, were published as journal articles, and started treatment no longer than an average of 5 days after symptom onset.

Mohan 2021 reported this outcome for inpatients at 14 days which was too short, and Kirti 2021 reported the outcome but without the time point of assessment. Those trials were clinically not comparable with trials reporting our predefined outcome and were therefore not eligible for meta‐analysis.

One trial comparing ivermectin plus standard of care to standard of care plus placebo in 73 participants with moderate disease reported participants discharged alive at day 28 ( Gonzalez 2021 ). In both groups, 27 participants were discharged alive at 28 days ( ). Ivermectin plus standard of care may have little or no effect on clinical improvement, assessed by the number of participants discharged alive at day 28 compared to standard of care plus placebo (RR 1.03, 95% CI 0.78 to 1.35; 1 trial, 73 participants; low‐certainty evidence). We downgraded the certainty of evidence one level for serious risk of bias and one level for serious imprecision due to few participants and a wide CI. Gonzalez 2021 had some concerns regarding risk of bias, was published as a preprint article, and did not state when they started treatment.

No trial reported data for participants with need for ICU admission or death at day 28. Two trials reported ICU admission at day 28 without the endpoint of death. Those trials did not take into account the competing risk of death in outcome measurement and were therefore not eligible for meta‐analysis ( Kirti 2021 ; Pott‐Junior 2021 ).

One trial in an inpatient setting reported worsening of clinical status at 14 days ( Mohan 2021 ), and one trial reported participants with new need for invasive mechanical ventilation at day 28 ( Kirti 2021 ), but without the competing endpoint of death. Those trials were clinically not comparable with trials reporting our predefined outcome and were therefore not eligible for meta‐analysis.

Two trials comparing ivermectin plus standard of care to standard of care plus/minus placebo reported data on clinical worsening, assessed by new need for invasive mechanical ventilation or death at day 28 for 118 participants with moderate disease ( Gonzalez 2021 ; Krolewiecki 2021 ). Seven participants in the ivermectin group and eight participants in the comparator group showed clinical worsening ( ). We are uncertain whether ivermectin plus standard of care reduces or increases clinical worsening, assessed by participants with new need for invasive mechanical ventilation or death compared to standard of care plus/minus placebo at day 28 (RR 0.82, 95% CI 0.33 to 2.04; 2 trials, 118 participants; very low‐certainty evidence). We downgraded the certainty of evidence one level for serious risk of bias and two levels for very serious imprecision due to few participants, very few events, and wide CI. One trial had some concerns regarding risk of bias, was published as a preprint article, and did not report time since symptom onset ( Gonzalez 2021 ). The sensitivity analysis including only the trial with low risk of bias, being published in a journal and started treatment early ( Krolewiecki 2021 ), estimated the intervention effect with even more imprecision at RR 1.55 (95% CI 0.07 to 35.89; 1 trial, 45 participants).

Three trials comparing ivermectin plus standard of care to standard of care plus/minus placebo reported data on mortality at day 28 for 230 participants with moderate disease ( Gonzalez 2021 ; Kirti 2021 ; Krolewiecki 2021 ). In the meta‐analysis, five participants died in the ivermectin group and nine participants in the comparator group ( ). We are uncertain whether ivermectin plus standard of care reduces or increases all‐cause mortality at 28 days compared to standard of care plus/minus placebo (risk ratio (RR) 0.60, 95% confidence interval (CI) 0.14 to 2.51; 3 trials, 230 participants; very low‐certainty evidence). We downgraded the certainty of evidence one level for serious risk of bias and two levels for very serious imprecision due to few participants, very few events, and wide CI. Two trials had some concerns regarding risk of bias ( Gonzalez 2021 ; Kirti 2021 ). The sensitivity analysis including only one trial with low risk of bias was not estimable due to zero events (1 trial, 45 participants). This equals the sensitivity analysis including only one trial starting treatment at a mean of 5 days after symptom onset ( Krolewiecki 2021 ). Again, we had to exclude Gonzalez 2021 and Kirti 2021 because they did not report time since symptom onset or started treatment late, respectively. One trial was published as a preprint article ( Gonzalez 2021 ). The sensitivity analysis including only trials published in a journal ( Kirti 2021 ; Krolewiecki 2021 ), estimated the intervention effect with even more imprecision at RR 0.15 (95% CI 0.01 to 2.80; 2 trials, 157 participants).

We used sensitivity analyses to test the robustness of meta‐analyses by excluding trials with overall high or some risk of bias, non‐peer‐reviewed trials, and trials that started ivermectin treatment late (more than 5 days after symptom onset): only one trial was not peer‐reviewed ( Gonzalez 2021 for inpatients); and we excluded three trials in the sensitivity analyses because they started treatment later than 5 days after symptom onset ( Gonzalez 2021 days not reported; Kirti 2021 with mean 6.9 ± 6.6 days; Pott‐Junior 2021 with median 8 (IQR 7 to 10) days), all other trials started treatment at a mean of 5 days after symptom onset. We did not perform sensitivity analyses regarding vaccination status, since most of the trials recruited non‐vaccinated participants before vaccines became available. I‐TECH 2022 and Bounfrate 2021 included vaccinated participants, however the proportion was either insignificant ( I‐TECH 2022 with 2% vaccination), or outcome data were not reported for the vaccinated subgroup ( Bounfrate 2021 ). According to the trial protocol of TOGETHER 2022 , vaccinated participants were eligible for inclusion, however there is no information whether any vaccinated people were included in the trial. History of SARS‐CoV‐2 infection was not investigated in the included trials.

We planned to investigate heterogeneity for the characteristics: dose, age and severity of the condition, within the different settings by subgroup analysis, if at least 10 trials per outcome had been available; due to insufficient trials, we were unable to perform this.

Six trials investigated ivermectin for treating COVID‐19 in an outpatient setting and contributed data to meta‐analyses ( Bounfrate 2021 ; Chaccour 2021 ; I‐TECH 2022 ; López‐Medina 2021 ; TOGETHER 2022 ; Vallejos 2021 ). All trials investigated participants with asymptomatic to mild COVID‐19. No trial followed up participants for more than 1 month. The main findings are summarized in .

Five trials investigated ivermectin for treating COVID‐19 in an inpatient setting and contributed data to meta‐analyses ( Gonzalez 2021 ; Kirti 2021 ; Krolewiecki 2021 ; Mohan 2021 ; Pott‐Junior 2021 ). All trials investigated participants with moderate COVID‐19, no trial investigated severe disease. Therefore, planned subgroup analyses for severity at baseline were not possible. No trial followed up participants for more than 1 month. The main findings are summarized in .

We identified key concerns for the outcome ‘any adverse events during the trial period’; the high risk of bias in this outcome measurement was caused by lack of blinding of the outcome assessors in one trial, contributing 13.8% weight to the meta‐analysis.

We identified some concerns across trials and per outcome for the outcomes 'symptom resolution: all initial symptoms resolved (asymptomatic) at day 14' and 'serious adverse events during the trial period', with 68.3% and 100% of weight in the meta‐analyses coming from trials with some level of concern due to lack of information on definition and measurement of the outcome ( Bounfrate 2021 ; Chaccour 2021 ), not prospectively registering the outcome ( Bounfrate 2021 ; Chaccour 2021 ), lack of blinding of outcome assessors ( I‐TECH 2022 ), or inappropriate analysis ( López‐Medina 2021 ). We had concerns for the outcome 'all‐cause mortality at day 28' due to inappropriate per‐protocol analysis in one trial with 2.3% weight in the meta‐analysis ( López‐Medina 2021 ). We assessed the outcome 'viral clearance at day 7' as having some concerns regarding risk of bias due to insufficient explanation for missing outcome data in one trial with 98.5% weight in the meta‐analysis ( TOGETHER 2022 ).

We have no concerns regarding risk of bias across trials for the outcomes ‘worsening of clinical status within 28 days: admission to hospital or death’, 'quality of life (physical component) at up to 28 days', and 'quality of life (mental component) at up to 28 days'; three low risk of bias trials contributed data to these results ( Bounfrate 2021 ; TOGETHER 2022 ; Vallejos 2021 ).

Key concerns across trials and per outcome were identified for the following outcomes: ‘any adverse events during the trial period’ due to lack of blinding of participants and outcome assessors for a patient‐reported outcome in two trials, 63.9% weight in the meta‐analysis ( Krolewiecki 2021 ; Pott‐Junior 2021 ), and 'viral clearance at day 7' due to an inappropriate per‐protocol analysis and missing outcome data in two trials, 54.7% weight in the meta‐analysis ( Kirti 2021 ; Pott‐Junior 2021 ).

For the outcome 'worsening of clinical status at day 28: participants with new need for invasive mechanical ventilation or death', 91.6% of weight in the meta‐analysis came from one trial ( Gonzalez 2021 ); we were concerned with insufficient information about allocation concealment and blinding of healthcare providers, and concerned that the protocol failed to define the time point of this outcome measurement.

We have at least some level of concern regarding risk of bias across trials for all outcomes included in the summary of findings tables. For the outcomes 'all‐cause mortality at day 28', 'improvement of clinical status at day 28: participants discharged alive' and 'serious adverse events during the trial period', we assessed all trials contributing estimable data to the meta‐analyses as having some concern for bias due to concerns across various domains.

In summary, 15 of the ongoing trials have passed their completion dates, i.e. up to mid‐2021, or the trial register did not contain any information on a planned completion date; about 50% (8/15) should have been completed more than 6 months ago, but none have published results, either in a trial registry or as full text.

Trials to prevent SARS‐CoV‐2 infection compare ivermectin with placebo; in general these trials have not yet started recruiting ( ACTRN12621001535864 ; {"type":"clinical-trial","attrs":{"text":"NCT04527211","term_id":"NCT04527211"}}NCT04527211 ; {"type":"clinical-trial","attrs":{"text":"NCT05060666","term_id":"NCT05060666"}}NCT05060666 ; PACTR202102848675636 ). Two of those trials should have already been completed ( {"type":"clinical-trial","attrs":{"text":"NCT04527211","term_id":"NCT04527211"}}NCT04527211 ; PACTR202102848675636 ), with the former trial indicating a completion date of more than 6 months ago ( {"type":"clinical-trial","attrs":{"text":"NCT04527211","term_id":"NCT04527211"}}NCT04527211 ). The trial investigating both treatment and prevention was planned to be completed more than 6 months ago, and has no information on recruitment status ( 2020‐001994‐66/ES ).

Three trials, all including less than 200 participants, were unclear whether they plan to investigate ivermectin for COVID‐19 treatment in an in‐ or outpatient setting; they are either still recruiting ( Ashraf 2021 ; {"type":"clinical-trial","attrs":{"text":"NCT04445311","term_id":"NCT04445311"}}NCT04445311 ), or not yet recruiting ( {"type":"clinical-trial","attrs":{"text":"NCT04510233","term_id":"NCT04510233"}}NCT04510233 ), although the completion date they initially stated in their registry entry was more than 6 months ago.

Nine inpatient trials investigate ivermectin plus standard of care versus standard of care plus/minus placebo for treatment of COVID‐19 ( 2021‐002024‐21/CZ ; CTRI/2020/05/025068 ; CTRI/2020/05/025224 ; IRCT20111224008507N5 ; IRCT20190417043295N2 ; {"type":"clinical-trial","attrs":{"text":"NCT04425707","term_id":"NCT04425707"}}NCT04425707 ; {"type":"clinical-trial","attrs":{"text":"NCT04836299","term_id":"NCT04836299"}}NCT04836299 ; {"type":"clinical-trial","attrs":{"text":"NCT04944082","term_id":"NCT04944082"}}NCT04944082 ; SLCTR/2021/020 ), with five of those using a placebo in the comparator group ( 2021‐002024‐21/CZ ; IRCT20111224008507N5 ; IRCT20190417043295N2 ; {"type":"clinical-trial","attrs":{"text":"NCT04836299","term_id":"NCT04836299"}}NCT04836299 ; SLCTR/2021/020 ). Trial sizes are small, with enrolment numbers mainly below 100. Only two trials plan to enrol more than 200 participants ( IRCT20111224008507N5 ; SLCTR/2021/020 ). {"type":"clinical-trial","attrs":{"text":"NCT04425707","term_id":"NCT04425707"}}NCT04425707 is still recruiting, although the planned completion date is more than 6 months ago. Two other trials have not started recruitment yet, although their completion date lies in the past ( {"type":"clinical-trial","attrs":{"text":"NCT04836299","term_id":"NCT04836299"}}NCT04836299 ; {"type":"clinical-trial","attrs":{"text":"NCT04944082","term_id":"NCT04944082"}}NCT04944082 ). Four trials do not indicate a planned completion date in their registry entry ( 2021‐002024‐21/CZ ; CTRI/2020/05/025068 ; CTRI/2020/05/025224 ; SLCTR/2021/020 ). For two trials, the planned completion date lies in the future ( IRCT20111224008507N5 ; IRCT20190417043295N2 ).

Nine trials were not sufficiently explicit in their protocol to allow us to make a final decision on eligibility. First, none of the following seven trials reported a clear description of the type of control intervention used as comparator ( 2020‐001971‐33/ES ; CTRI/2020/04/024948 ; CTRI/2020/06/025960 ; {"type":"clinical-trial","attrs":{"text":"NCT04351347","term_id":"NCT04351347"}}NCT04351347 ; {"type":"clinical-trial","attrs":{"text":"NCT04374019","term_id":"NCT04374019"}}NCT04374019 ; {"type":"clinical-trial","attrs":{"text":"NCT04746365","term_id":"NCT04746365"}}NCT04746365 ; {"type":"clinical-trial","attrs":{"text":"NCT04891250","term_id":"NCT04891250"}}NCT04891250 ). Additionally, for one of those trials, it was unclear if a RT‐PCR‐confirmed SARS‐CoV‐2 infection was required for inclusion ( {"type":"clinical-trial","attrs":{"text":"NCT04351347","term_id":"NCT04351347"}}NCT04351347 ). Similarly, two trials investigating prevention were not well‐defined regarding the inclusion criteria of high‐risk exposure to an index patient ( ISRCTN90437126 ; {"type":"clinical-trial","attrs":{"text":"NCT04891250","term_id":"NCT04891250"}}NCT04891250 ). Finally, for another trial, we could not evaluate the actual rationale or the considered patient population due to inconclusive PICO details ( IRCT20200408046987N3 ).

Three trials have been terminated without publication of interim results so far ( 2020‐005015‐40/SK ; {"type":"clinical-trial","attrs":{"text":"NCT04602507","term_id":"NCT04602507"}}NCT04602507 ; PACTR202102588777597 ). Of those, one trial took place in an inpatient setting ( {"type":"clinical-trial","attrs":{"text":"NCT04602507","term_id":"NCT04602507"}}NCT04602507 ), one in an inpatient as well as prevention setting ( PACTR202102588777597 ), and one in an outpatient setting ( 2020‐005015‐40/SK ). One trial compared ivermectin plus standard of care to standard of care plus placebo ( 2020‐005015‐40/SK ) and two compared ivermectin plus standard of care to standard of care alone ( {"type":"clinical-trial","attrs":{"text":"NCT04602507","term_id":"NCT04602507"}}NCT04602507 ; PACTR202102588777597 ).

Of those, three trials were generally eligible for inclusion but did not pass the research integrity check ( Aref 2021 ; {"type":"clinical-trial","attrs":{"text":"NCT04407507","term_id":"NCT04407507"}}NCT04407507 ; {"type":"clinical-trial","attrs":{"text":"NCT04673214","term_id":"NCT04673214"}}NCT04673214 ), as relevant information to assure trustworthiness was missing. Contact with the trialists either yielded no or only partial responses that could not fully clarify the issue at the time of completing this review update.

TOGETHER 2022 measured health‐related quality of life in outpatients at 28 days on a standardized scale, the PROMIS Global‐10 scale, separated in a physical and mental component. No trial measured quality of life in the inpatient setting and no trial followed up participants for more than 30 days in either setting.

For the outpatient setting, several primary outcomes (as defined by the new outcome set of this review) were reported by all included trials. Five trials reported mortality at 28 or 30 days ( Bounfrate 2021 ; Chaccour 2021 ; I‐TECH 2022 ; TOGETHER 2022 ; Vallejos 2021 ); López‐Medina 2021 reported this outcome at 21 days, however as those time points lie closely together, especially in respect to the patient setting, we considered pooling the data clinically reasonable. Serious adverse events and any adverse events during the trial period were reported by Bounfrate 2021 at 30 days, by Chaccour 2021 and I‐TECH 2022 at 28 days, by López‐Medina 2021 at 21 days, and by Vallejos 2021 until the participants were declared SARS‐CoV‐2 negative, which was at a median of 12 days. The trials used slightly varying, though equally relevant definitions, for both outcomes. As for the time point, we decided it was clinically reasonable to pool the available data as 'during the trial period', because the intervention was not administered in any of the trials for more than 5 days.

Viral clearance was reported by three trials: Kirti 2021 reported this outcome for day 6, Pott‐Junior 2021 for day 7, and Mohan 2021 for day 5. We judged these time points as eligible and clinically reasonable for pooling the review's outcome of viral clearance at day 7. Mohan 2021 also reported eligible data for day 3, however we judged the trial's data for day 7 as unusable because no result was available for many participants.

For the inpatient setting, no new trials contributed data to the primary outcomes of this review update compared to the previous review version. However, meta‐analyses changed due to the adjusted primary outcome set. For each outcome, data were available from three trials at the most. We were able to pool data for mortality (measured at 28 days in Gonzalez 2021 and Kirti 2021 and 30 days in Krolewiecki 2021 ) with clinical reason. Data usable to assess the outcomes, clinical worsening ('participants with new need for invasive mechanical ventilation or death') and clinical improvement ('participants discharged alive') at day 28 were reported for eligible time points by two trials ( Gonzalez 2021 ; Krolewiecki 2021 ‐reporting for 30 days) and one trial ( Gonzalez 2021 ), respectively. Any adverse events during the trial period were reported by Krolewiecki 2021 at 30 days, by Mohan 2021 at 14 days, and by Pott‐Junior 2021 at 28 days. Two of those also measured serious adverse events, Krolewiecki 2021 at 30 days and Mohan 2021 at 14 days. The trials used slightly varying, though equally relevant definitions, for both outcomes. As for the time point, we decided it was clinically reasonable to pool the available data as 'during the trial period', because the intervention was not administered in any of the trials for more than 5 days.

Most trials started treatment at a mean of 5 days after symptom onset. Kirti 2021 and Pott‐Junior 2021 had the longest time since symptom onset with a mean of 6.9 (SD 6.6) days and a median of 8 (IQR 7 to 10) days. Gonzalez 2021 did not report on time since symptom onset.

Eight trials were conducted before the global vaccination campaigns. Of the two trials including vaccinated participants, Bounfrate 2021 reported an overall vaccination rate of about 3% and I‐TECH 2022 included over 50% of participants with two doses of vaccine and about 30% of unvaccinated participants. The authors of TOGETHER 2022 stated that vaccinated, as well as unvaccinated participants, were eligible for the trial, but did not provide further details on the vaccination status of included participants.

The trials partially reported comorbidities and relevant risk factors for severe COVID‐19, such as obesity, diabetes, respiratory diseases, hypertension, and immunosuppression (see Characteristics of included studies table). I‐TECH 2022 only included patients aged 50 years and above with at least one prespecified comorbidity. TOGETHER 2022 defined age (> 50 years) or at least one prespecified comoridity as inclusion criteria. Two trials excluded existing comorbidities and specified them in the inclusion and exclusion criteria ( Chaccour 2021 ; Krolewiecki 2021 ). One trial reported no data on risk factors in their publications or trial reports ( Pott‐Junior 2021 ).

The overall mean age in the trials was 45 years. Chaccour 2021 included the youngest participants with a median age of 28 years. I‐TECH 2022 included the oldest participants with a mean age of 63 years. The mean proportion of women in all included trials was 44%. The lowest proportions of men were in López‐Medina 2021 and TOGETHER 2022 with 42% men, while Kirti 2021 included the highest proportion with 72% men.

We held all potentially eligible trials with disparities in the reporting of the methods and results in ‘awaiting classification’ until the trial authors respond to our information requests. One trial awaiting classification in the previous review version ( {"type":"clinical-trial","attrs":{"text":"NCT04407507","term_id":"NCT04407507"}}NCT04407507 ), and one trial with newly‐identified published results ( {"type":"clinical-trial","attrs":{"text":"NCT04673214","term_id":"NCT04673214"}}NCT04673214 ), have not been published as full texts yet, and relevant information assuring research integrity is missing from the trials' registry record. Aref 2021 described their randomization method insufficiently in the journal publication, therefore the actual trial design remained unclear. We requested clarification regarding information on randomization methods and trial results: {"type":"clinical-trial","attrs":{"text":"NCT04602507","term_id":"NCT04602507"}}NCT04602507 investigators responded that they would share any data/information once the trial is published; {"type":"clinical-trial","attrs":{"text":"NCT04673214","term_id":"NCT04673214"}}NCT04673214 investigators could not clarify all outstanding issues in time; and Aref 2021 did not respond at all. We will re‐evaluate trials awaiting classification in the next review update.

One trial awaiting classification in the previous review version was retracted in the meantime ( Samaha 2021 ); we excluded the trial in this review update. We excluded three included trials ( Ahmed 2020 ; Kishoria 2020 ; Podder 2020 ), and one trial awaiting classification ( Faisal 2020 ) from the previous review as they were not registered in a national or international trials registry. Before making the final decision on this, we contacted the trial authors to make sure we had not overlooked any registration. Three included trials from the previous review ( Chachar 2020 ; Okumuş 2021 ; Shah Bukhari 2021 ), and two trials with newly‐identified full‐text publications ( Abd‐Elsalam 2021 ; Biber 2021 ) were retrospectively registered; i.e. the date of first enrolment of participants was before the date of first protocol submission to the trials register. We used the date of submission instead of the date first posted to exclude a possible delay in the registration process at this point in the pandemic. We excluded these retrospectively registered trials also. One included trial from the previous review turned out to be a non‐randomized trial ( Shouman 2021 ). The authors described the method used for randomization via personal communication, which we then assessed as non‐randomized alternate allocation; we excluded this trial from this review update.

We conducted the literature search again completely without date restriction; this resulted in 567 records. We identified a further two records from a hand search of reference lists. Since the date of last search (16 December 2021) up to February 2022, we used the CCSR to monitor newly‐published results of RCTs on ivermectin on a weekly basis. In addition, we found one trial that had provided data via personal communication had been published as a journal article during conduction of the review update ( I‐TECH 2022 ). Thus, we evaluated 570 records overall. The 22 records we had identified by hand search in the previous review, appeared in searched databases by the time of this updated search, and could be deduplicated. After removing duplicates, 382 records remained. During title and abstract screening, we judged 200 records as irrelevant as they did not meet the prespecified inclusion criteria. We proceeded to full‐text screening with 182 records, of which 39 records were newly identified in the updated search and 143 records that had already been screened in the previous review version had to be reassessed for eligibility. The re‐evaluation was necessary because the research integrity assessment was introduced as a new eligibility criteria for trials, and additionally, previously ongoing trials had to be reassessed if new information had become available in the meantime. Decisions from the original review version that were changed due to assessment of the trials’ research integrity can be found in . We considered published full texts in journals or on preprint servers or, if these were unavailable, entries in trial registers. We excluded 55 trials (84 records) with reasons after full‐text assessment. We identified 31 ongoing trials (37 records) and 28 trials (30 records) awaiting assessment. In February 2022 we set the deadline for inclusion of newly‐published trial results for this review update. Hence, after initially closing the trial pool for this review update, we identified one trial with more than 1000 participants, previously classified as ongoing, that published its results in March 2022. We included this trial in the review without an additional systematic search, resulting in 11 trials (32 records) that met our eligibility criteria and enabled us to perform qualitative syntheses and meta‐analyses (quantitative syntheses). The search process is shown in .

Discussion

Summary of main results

For this review update, we reappraised eligible trials for research integrity. We excluded 7 of the 14 trials included in the previous review version; six were not prospectively registered and one turned out to be non‐randomized. Four trials of the updated search passed the research integrity assessment and were eligible for this review. Finally, this review included 11 trials with 3409 participants investigating ivermectin plus standard of care compared to standard of care plus/minus placebo. Investigating treatment of COVID‐19, five trials were conducted in inpatient settings with moderate COVID‐19 (WHO 4 to 5) only and six trials in outpatient settings with mild COVID‐19 (WHO 1 to 3). No trial investigated ivermectin for the prevention of SARS‐CoV‐2 infection. The included trials contributed 44 trial results to the review, about one‐half of which we assessed as having some concerns or high risk of bias. The main findings of this review are summarized in   (treatment; inpatients) and   (treatment; outpatients). The number of trials per outcome increased compared to the previous review version, especially in the outpatient setting. For the inpatient setting though, there were still no more than three trials per outcome providing useful data for our updated outcome set.

Ivermectin showed no evidence of an effect on increasing or decreasing mortality at 28 days, the most important outcome during this pandemic, neither in inpatients (3 trials) nor outpatients (6 trials). The certainty of evidence for this finding was very low and moderate, respectively. Since the last review, the certainty of evidence increased for mortality in outpatients from very low to moderate. 

For all other outcomes relevant for inpatients with moderate disease, such as risk of clinical worsening, being discharged alive, adverse or serious adverse events, and viral clearance, ivermectin showed no evidence of an effect, neither for improving nor worsening the respective outcome. The certainty of evidence for those findings varied from very low to low. Compared to the previous review version, certainty of evidence for any adverse events and viral clearance at day 7 in the inpatient setting increased from very low to low in this update. 

For the outpatient setting, the relevant outcome of admission to hospital or death as well as quality of life, that were not reported by any trial in the previous review version, could be evaluated in this update. Overall, for all the outcomes relevant for outpatients with mild disease, such as risk of needing hospitalization, resolving symptoms, adverse or serious adverse events and viral clearance, ivermectin showed no evidence of an effect neither for improving nor worsening the respective outcome. The certainty of evidence for all of those findings was low. With high certainty, we found that ivermectin showed no effect on quality of life for the outpatient setting.

No trial investigated ivermectin for the prevention of SARS‐CoV‐2 infection. Hence, no evidence could be found for postexposure prophylaxis in this matter. 

Overall completeness and applicability of evidence

First, with the new outcome set in this update, we mainly addressed the issue of competing outcome risk. We combined outcomes that represent clinical worsening with the outcome of death which would allow evidence on ivermectin to become more unambiguous and patient‐relevant.

Four newly‐included trials for the outpatient setting increased certainty of evidence on ivermectin for this purpose compared to the previous review version. Overall, the included trials investigated participants with COVID‐19 at WHO 1 to 3 and WHO 4 to 5. Therefore, findings of this review are transferable to patients with COVID‐19 at mild to moderate stages. In this update, no trials investigated ivermectin for severe COVID‐19 (WHO 6 to 9). Considering the proposed mode of action, no effect of the drug would be expected if given at such a late stage of the disease. Hence, we do not consider this to be an evidence gap that needs to be closed. Moreover, with few exceptions, most included trials reported treatment initiation within a mean of 5 days after symptom onset, which is in line with the propagated hypothesis of ivermectin's inhibitory effect on virus replication in early stages of the disease. 

In contrast to the hype around ivermectin's potential to prevent a SARS‐CoV‐2 infection after high‐risk contact, no RCT investigating this purpose has been published since the previous review version. Most trials were conducted before any form of vaccination was available, leading to 93% of participants across trials knowingly not being vaccinated. Therefore, we could not assess the influence of vaccination status in this review update. Equally, we could not identify any evidence on the effect of ivermectin on the newly‐emerging Omicron variant.

Overall, most trials reported a mean age far below 60 years (overall mean age was 45 years with a mean range from 28 to 63 years). Additionally, in the inpatient setting, trials included people with few or no comorbidities. Considering age and pre‐existing conditions as the most important risk factors for developing severe COVID‐19 and complications from the disease, the current evidence for inpatients is not applicable to patients who are at most risk of suffering COVID‐19 with serious consequences such as death or need for mechanical ventilation. In the outpatient setting, applicability of the evidence improved compared to the previous review version, since three of six trials included large proportions of participants with comorbidites, such as obesity and hypertension. 

COVID‐19 vaccinations provide the most reliable and safest protection against the SARS‐CoV‐2 virus and progression to severe disease, however due to global inequity, not every region of the world has unlimited access to vaccinations. Therefore, it is to be expected that countries with low and middle healthcare expenditure, focus research efforts on repurposing of drugs. Accordingly, six trials were conducted in Latin America, three in Asia, and only two in Europe. In some of these countries, uncontrolled ivermectin use is making it difficult to test the effectiveness of the antiparasite drug against SARS‐CoV‐2 (Rodríguez‐Mega 2020).

All trials administered ivermectin per mouth, but the doses and durations of administration varied. We set 200 µg/kg/day orally as the low dose based on the dosing recommendation for strongyloidiasis (WHO 2019). Five of the 11 trials used low doses in at least one trial arm. All other trials utilized higher doses, either in a single dose or over 2 to 5 days. Due to the small number of trials per outcome, we did not perform any subgroup analyses with low versus high doses, and no evidence or clinical implication can be obtained regarding a certain dosing regimen. 

Overall, although we were able to increase the certainty of evidence in this review update, we are still in need of good‐quality trials in relevant populations to obtain evidence that would justify the use of ivermectin in regular patient care. During the literature search, we found two major ongoing trials soon to be completed (ISRCTN86534580; {"type":"clinical-trial","attrs":{"text":"NCT04510194","term_id":"NCT04510194"}}NCT04510194), which might contribute evidence for patient treatment, especially in the outpatient setting.

We found no trials that compared ivermectin to an active comparator with confirmed efficacy. Three of the 11 trials had an open‐label design and used standard of care alone as comparators. All other trials were placebo‐controlled trials. Standard of care must be the same between the individual trials' arms. There are several trials circulating that investigate various concomitant medications (e.g. doxycycline, hydroxychloroquine, azithromycin, zinc) in addition to ivermectin. Due to unproven efficacy and possible adverse effects, these comparisons may confound the assessment of the efficacy or safety of ivermectin, and we considered the inclusion of such combination therapies inappropriate. The same accounts for the comparison of ivermectin with an active comparator that has no proven efficacy in COVID‐19. Although those types of interventions (e.g. hydroxychloroquine) were possibly used at a certain point of the pandemic with the best intentions, their use was never supported by actual evidence, and they have potential adverse effects (Singh 2021). As we do not know the effect of many of those experimental comparators in people with COVID‐19, consequently no reliable evidence for ivermectin can be obtained from those comparisons either.

Finally, we found 31 ongoing trials, of which around 50% (15/31) should have been completed by mid‐2021 or else no planned completion date was stated. Twenty‐eight trials are awaiting classification of which 13, that we judged as potentially eligible, have already been completed without publication of results. When conducting the previous review version, we expected many of these trials to be published by the end of 2021. By contrast, we discovered that 70% of the completed trials (9/13) and about 50% (8/15) of ongoing trials should have been completed more than 6 months ago, but their results have not been published in trial registries, preprint servers or journals. After this amount of time, it seems unlikely that trial data will become available from those trials, for whatever reasons. Given those numbers, we think it will be necessary to consider publication bias in the next review update. 

Certainty of the evidence

The certainty of evidence for prioritized outcomes presented in the summary of findings tables ranged from very low to high ( ;  ). Compared to the previous review version, the certainty of evidence increased one level for any adverse events and viral clearance at day 7 for inpatients and two levels for all‐cause mortality in outpatients. New outcomes for the review update were serious adverse events (in both settings), new need for invasive mechanical ventilation or death (inpatients), as well as quality of life, and admission to hospital or death (outpatients).

For the summary of findings tables and assessment of the certainty of evidence according to Schünemann 2020, we used the results from analysis of our primary outcome sets. We assessed one‐half of the trial results at overall low and one‐ninth at overall high risk of bias. This is a considerable improvement compared to the previous review version, in which one‐third of trial results were at overall high risk of bias. In the current update, after assessing trials for research integrity, we eliminated most of the trial results we had assessed at high risk of bias in the previous review version. 

On the one hand, this update has resulted in four newly‐included outpatient trials, contributing 2452 new participants to the review. On the other hand, the introduction of our research integrity assessment tool served to improve quality and trustworthiness of the included trial pool. Through this tool, we excluded six of the 14 trials included in the previous review version, because they were not prospectively registered. Five out of six trials reported relevant outcomes (Ahmed 2020; Kishoria 2020; Okumuş 2021; Podder 2020; Shah Bukhari 2021); we rated four of these five trials at high risk of bias for all outcomes (Kishoria 2020; Okumuş 2021; Podder 2020; Shah Bukhari 2021). Only one trial contributed data to three outcomes in the respective summary of findings table (Ahmed 2020). In the previous review version, we excluded high risk of bias trials from the primary analysis, with the aim to remove biased data and untrustworthy trials. However, to be transparent, all trials were presented in a secondary analysis. After all, the result of the research integrity assessment – inclusion of prospectively registered RCTs only ‐ was comparable to the exclusion of high risk of bias trials from the primary analysis. Nevertheless, in this review update we downgraded the certainty of evidence one level due to serious risk of bias for all inpatient outcomes and four of nine outpatient outcomes because we assessed at least one of the results as having 'some concerns' of bias. Details of the risk of bias assessments per outcome are reported in Risk of bias in included studies.

Another limitation for the certainty of evidence was the low number of participants, events, or both leading to wide CIs and uncertainty of the estimated effects. We downgraded all outcomes included in the summary of findings tables for inpatients one or two levels for imprecision. In the outpatient setting, the number of analysed participants increased for all outcomes in this update. This improved the quality of the evidence, especially for mortality compared to the previous review update. For the newly‐available outcome of 'quality of life', results were precise, so we could grade certainty of the evidence as high. However, due to few events resulting in wide CIs, we had to downgrade one level for imprecision for several outpatient outcomes.

Heterogeneity was no reason to downgrade the certainty of evidence for treatment of inpatients. This is mainly due to the small number of trials per meta‐analysis. In the outpatient setting, we downgraded certainty of evidence one level for serious inconsistency in three outcomes with moderate to substantial heterogeneity. Those were 'admission to hospital or death within 28 days' (I2 = 44%), 'all initial symptoms resolved at day 14' (I2 = 57%), and 'any adverse events during the trial period' (I2 = 80%).

We did not downgrade any of the outcomes included in the summary of findings tables for indirectness. In all cases, the effect estimates were based on comparisons of interest, on the population of interest, and on outcomes of interest. In the current phase of the pandemic, it is still difficult to reliably assess the risk of publication bias. In this update, we still did not downgrade for publication bias for any outcome. However, as explained above this will probably change in future updates of this review.

Potential biases in the review process

This review aimed to provide a complete and updated evidence profile for ivermectin with regard to efficacy and safety for postexposure prophylaxis of SARS‐CoV‐2 infection and treatment of COVID‐19 based on current Cochrane standards (Higgins 2020a).

The review team was part of the German research project 'CEOsys' (COVID‐19 Evidence‐Ecosystem) until 31 December 2021. CEOsys is a consortium of clinical and methodological experts supported by the German Federal Ministry of Education and Research to synthesize clinical evidence during this global pandemic. The medical information specialists of this consortium carried out a rigorous search of electronic databases, including preprint servers and clinical trial registries, to identify the complete extent of published and ongoing trials on this topic. Additionally, we screened reference lists of included trials and compared our search results with those from the living network meta‐analysis (e.g. COVID‐NMA Working Group). Considering it a justifiable compromise between being as up to date as possible in the dynamic of this pandemic and reasons of practicability, we set February 2022 the deadline for inclusion of newly published trial results for this review update. Hence, after initially closing the trial pool for this review update, we identified one trial with more than 1000 participants, previously classified as ongoing, that published its results in March 2022. Therefore, we are confident that we have identified all relevant trials, and we continue to monitor ongoing trials, as well as full publication of preprints closely, following the publication of this review update.

Members of the CEOsys group established and performed a Cochrane Living Systematic Reviews Series on different interventions for treatment of COVID‐19 (Ansems 2021; Kreuzberger 2021; Mikolajewska 2021; Popp 2021c; Stroehlein 2021; Wagner 2021). In accordance with this review series, we updated our review's outcomes to overcome competing risks. We added outcomes for inpatients and outpatients that aim to simultaneously capture all participants of the population with clinical worsening and all participants with clinical improvement. This was possible by using composite outcomes, e.g. combining 'new need for invasive mechanical ventilation' and 'death' as clinical worsening for inpatients, and combining 'admission to hospital' and 'death' for outpatients. Clinical improvement for inpatients was represented by the 'number of participants discharged alive within the same time period' used for clinical worsening, and for outpatients as 'complete resolution of initial symptoms'.

We sent data requests to trial authors if parts of the new outcome set were reflected in the respective trial outcomes. Equally, we contacted trial authors if their publication included unclear or inconclusive information or in case of missing information, especially for assessing research integrity. Unfortunately, not all attempts at gathering data were successful; details of communication with authors are provided in the Characteristics of included studies table.

Almost all the trials that were only available as preprints in the previous review version, were published as peer‐reviewed journal publications in the meantime. Compared to five preprints in the previous review, we included only one non‐peer‐reviewed article in this update (Gonzalez 2021). We are aware that preprint articles may change following peer‐review. Nevertheless, we are convinced that including all eligible data in a highly dynamic situation, such as the COVID‐19 pandemic, is crucial to be up to date and to provide timely information on potentially promising treatment options. We were unable to judge the eligibility of three trials with published results due to inconsistencies in trial descriptions (Aref 2021; {"type":"clinical-trial","attrs":{"text":"NCT04407507","term_id":"NCT04407507"}}NCT04407507; {"type":"clinical-trial","attrs":{"text":"NCT04673214","term_id":"NCT04673214"}}NCT04673214). We contacted the corresponding authors to clarify questions, but we did not receive a satisfying response at the time of review publication. We classified another 13 completed trials as 'awaiting classification' because they are eligible, but have not yet published results appropriately. Additionally, 31 potentially eligible trials are still ongoing. In the face of this immense amount of potential upcoming data, it could be considered that conclusions of a future update may differ from those of the present review. However, it should be kept in mind that a number of trials never actually publish results, as described in Overall completeness and applicability of evidence. 

None of the members of the review author team has any affiliation with any stakeholder group who favours or disapproves of ivermectin or the comparators used in relevant trials.