Discussion
At present, randomized controlled trial (RCT) data on efficacy of fluvoxamine in prevention of severe forms of COVID-19 in infected individuals are modest and burdened with uncertainty2. In particular, two largest RCTs1,21 yielded ambiguous results. In Stop COVID 221 (terminated early for technical reasons), mildly symptomatic, adult, non-vaccinated COVID-19 outpatients were commenced on an early (within 7 days since the COVID-19 diagnosis) 15-day fluvoxamine regimen (2x100 mg to 3x100 mg/day) (n=272) or placebo (n=275): 15-day risks of the primary outcome (hospitalization or a new onset hypoxemia) or of hospitalization appeared similar in the two arms (4.8% fluvoxamine vs. 5.4% placebo and 4.0% fluvoxamine vs. 4.4% placebo, respectively).3,21 In a subsequent larger TOGETHER trial1 with closely similar patient characteristics, early commenced fluvoxamine (2x100 mg over 10 days) (n=741) appeared superior to placebo (n=756) in respect to the 28-day risk of the primary outcome (hospitalization or emergency room stay longer than 6 hours) or (somewhat less so) regarding hospitalizations (11.0% fluvoxamine vs. 16.0% placebo and 10.0% fluvoxamine vs. 13.0% placebo, respectively)1. Under specific circumstances, non-randomized studies of interventions might be comparable to RCTs in terms of validity and accurracy in detecting a causal treatment effect.22 Treatment of early COVID-19 with fluvoxamine is a specific setting in which this kind of inference based on observational data is highly questionable. Given that in real life fluvoxamine is prescribed exclusively to alleviate specific psychiatric symptoms, the source population for the “treatment-control” comparison of interest (in the present study - Group A vs. Group B) is unavoidably limited to people who, at the time of COVID-19 diagnosis, suffer conditions requiring antidepressant/anxyolytic treatment. This also means that in contrast to a “standard” situation in which treatment is commenced only after the condition to be treated has occurred, “exposure/treatment” of interest (fluvoxamine) is likely in place at the time of occurrence of COVID-19. Theoretically, this may generate bias: if pre-existing mood disorders/exposure to fluvoxamine affect the risk of COVID-19 infection, then by inclusion of only COVID-19 diseased people one conditions on a post-baseline factor. There is rather sound evidence that mood disorders as such do not affect susceptibility to COVID-19 infection.23 However, it is unknown whether this holds also for exposure to fluvoxamine at the time of the contact with the virus. Next, prescription issuance is a proxy for “exposure” and actual treatment cannot be directly measured. The present definitions of “exposed” (Group A, implying a drug supply around timing of COVID-19 diagnosis sufficient for at least 3 months of treatment) and of “unexposed” subjects (Group B, no prescriptions issued between 6 months prior to and 21 days after the COVID-19 diagnosis) appear reasonable, but fluvoxamine doses in the approved indications might sometimes be lower than those suggested for early COVID-19 treatment.13 Therefore, in general, observational data could inform about the effect of fluvoxamine in early COVID-19 if one would consider as reasonable several assumptions: that what is observed in people with psychiatric difficulties is applicable in general; that exposure to fluvoxamine does not affect susceptibility to COVID-19 infection; and that being prescribed with fluvoxamine around the time of COVID-19 diagnosis indicates use of 100-300 mg/day fluvoxamine in the early phases of COVID-19 infection. Under such circumstances, the present data, for what it is worth, is more compatible with the Stop COVID 23,21 results than with TOGETHER1 trial results.
We used routinely collected adminsitrative data and not a dedicated pre-planned research database. As a consequence, some information was inherently missing (e.g., actually delivered treatment and presence/severity of symptoms at COVID-19 diagnosis), and some inaccurracies in identification of exposures, comorbidities and outcomes cannot be excluded. We believe, however, that if present, such inaccurracies were not sources of a relevant bias: i) it does not seem reasonable to assume that their occurrence was “prejudiced” in respect to (non)-issuance of fluvoxamine (or any other) prescriptions; ii) data on key variables such as age, sex, vaccination status, date of COVID-19 test/test result or diagnosis were missing or erroneously entered in only 0.38% of the identified COVID-19 diagnoses (Figure 1) indicating that if present, inaccurracies/chance errors were minor; iii) in Croatia, prescriptions are issued exclusively within the primary healthcare network, and each prescription bears an ATC code and an ICD-10 code. Moreover, for specialists consultations and work-up, patients need to be referred by the primary healthcare physicians who need to record the feedback information. All such acitivities are automatically entered into the Central Health Information System (CEZIH) (Figure 1). We also left a period of a minimum one year + 2 months (from January 1 2019 to the first COVID-19 case in February 2020) to precede the index COVID-19 diagnosis not to miss entries related to comorbidities that did not require recent presecriptions or other medical procedures. Hence, likely, no relevant comorbidity or treatment was missed; iv) incidence of all outcomes was within the expectations having in mind published data24, 25, which in a way provides external validation of the present observations. Considering raw data, 30-day all-cause hospitalization was closely similar in Group A and Group B patients (around 12.0%) (Figure 2), and the two subsets were also closely similar regarding age and comorbidities (Appendix, Table A5). Incidence was twice lower in Group C patients (5.2%) – in comparison to Group A (Appendix, Table A6) or Group B (Appednix, Table A7) patients, they were younger and considerably less burdened with comorbidities (e.g., Charlson Comorbidity Index was lower, all individual comorbidities were considerably fewer and there was no psychiatric comorbidity in Group C patients). The overall incidence of 6.9% (across all three subsets) at the average age of 46.5 years is in agreement with expected 4.3% to 8.5% hospitalizations among people aged 40-49 years who test positive for COVID-19.24Although one could consider all hospitalizations that occur within a month since the COVID-19 diagnosis as “COVID-19-related”, we defined a separate outcome where COVID-19 was the lead or at least one of the discharge diagnoses (implying that COVID-19 could have triggerred/worsened some underlying condition). It seems reasonable to assume that these were the “severe” or “critical” patients – Group A and Group B (around 3.3%) were again similar and incidence was (expectedly) much lower (0.94%) (Figure 2) in the younger and considerably less comorbid Group C patients. The overall incidence of 1.5% is within the range of the recently reported expected incidence of severe or critical disease in 30-50-year olds who tested positive for COVID.19 (1.2-2.5%).25 In line with the other two outcomes, a similar Group A/B vs. C relationship was observed regarding mortality (3.7-4.4% vs. 1.05%) (Figure 2). The overall incidence of 2.5% is in line with the ratio of cumulative COVID-19-confirmed deaths and COVID-19 confirmed cases in Croatia up to October 31, 2021.26 Of notion, (weighted) incidence of all outcomes, particularly of COVID-19-related hospitalizations and mortality, was lower in all matched sets than in the raw data (Figure 3 in comparison to Figure 2). This is due to the fact that we employed exact matching on a number of covariates and matches were found mainly among less comorbid subjects. Overall, it appears safe to conclude that we were able to resonably accurrately capture exposures, comorbidities, cotreatments and outcomes, and to adequatly control confounding by accounting for a number of known relevant epidemiological, comorbidity and co-treatment covariates. Under these circumstances, direct comparisons of Group A to Group B patients and to Group C patients, and combined direct and indirect comparisons of A and B patients consistently yieled relative risks for all three outcomes closely around unity or slightly above unity, i.e., we observed no estimate that would go “in favor” of the fact of being prescribed fluvoxamine around the time of COVID-19 diagnosis.
In conclusion, the present nationwide matched cohort study strongly suggests that outpatients prescribed with fluvoxamine around the time of COVID-19 diagnosis are not at a reduced risk of subsequent hospitalizations or death compared to their peers suffering similar psychiatric difficulties but not prescribed with fluvoxamine, or as compared to their peers free of psychiatric difficulties and respective treatments. Considering the specifics of the setting, present data could be viewed informative about efficacy of early fluvoxamine treatment in COVID-19 outpatients to prevent disease progression only under several strong assumptions. In this context, present observations are more compatible with trial data that failed to demonstrate a practically relevant benefit of fluvoxamine treatment than with the data that supprot efficacy of fluvoxamine in this setting.