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.