Placebo controlled trials in neuromyelitis optica are

Multiple Sclerosis and Related Disorders 4 (2015) 536–545

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Multiple Sclerosis and Related Disorders journal homepage: www.elsevier.com/locate/msard

Review article

Placebo controlled trials in neuromyelitis optica are needed and ethical Bruce A.C. Cree University of California San Francisco, 675 Nelson Rising Lane, Box 3206, San Francisco, CA 94110, United States of America

art ic l e i nf o

a b s t r a c t

Article history: Received 13 March 2015 Received in revised form 15 April 2015 Accepted 30 July 2015

Currently, there are no approved treatments for NMO. All therapeutic studies in NMO have been either small, retrospective case series or uncontrolled prospective studies. Such studies are susceptible to inherent biases. As a consequence, conclusions regarding efficacy and safety from these studies may be erroneous. The optimal method for assessing therapeutic efficacy is the prospective, controlled trial with random treatment assignment that has the potential to control for multiple sources of bias. There is a significant unmet need for well-designed clinical trials in NMO. Successfully conducted, well-controlled NMO trials that show proof of benefit will lead to regulatory approval and subsequent acceptance by payers resulting in broad therapeutic availability. The most direct method to prove efficacy is to compare an active treatment vs. no treatment or placebo control. However, because of the devastating nature of the disease some clinicians are reluctant to expose potential study patients to the risk of no treatment. The primary ethical concern in the case of placebo-control in NMO clinical trials rests on the relative merits of answering the scientific question regarding efficacy compared to the relative risk of exposure to harm in the placebo-control group. This article outlines the case for clinical equipoise in NMO by addressing the uncertainty regarding the relative scientific and clinical merits of current empirically used treatments and showing that a placebo arm is consistent with competent medical care. Because no currently available treatment has proven benefit, and because all therapies are known to potentially cause harm, placebo-control is not only ethical but is in some ways preferable to active comparator or add-on study designs. Without well-designed, placebo-controlled trials, NMO patients may not have access to new treatments and will never know whether the therapies that they may be currently taking have risk to benefit profiles that clearly favor their use. & 2015 The Authors. Published by Elsevier B.V. This is an open access article under the CC BY-NC-ND license (http://creativecommons.org/licenses/by-nc-nd/4.0/).

Keywords: Neuromyelitis optica Devic's disease Aquaporin 4 Placebo-control Clinical trial Ethics Equipoise

Contents 1.

Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1.1. Methodological weakness in existing NMO studies . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1.2. The need for randomized controlled trials . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1.3. The case for no treatment . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1.4. “Standard of care” for NMO . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1.5. Is there clinical equipoise? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1.6. The case for and against active comparators . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1.7. Combination therapy or add-on studies . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1.8. The moral hazard of non-participation. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1.9. Will NMO clinical trials harm patients? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1.10. Does disease severity or rarity matter with respect to placebo control? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1.11. Study design considerations in placebo controlled NMO trials . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . Conclusions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . References . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

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E-mail address: [email protected] http://dx.doi.org/10.1016/j.msard.2015.07.017 2211-0348/& 2015 The Authors. Published by Elsevier B.V. This is an open access article under the CC BY-NC-ND license (http://creativecommons.org/licenses/by-nc-nd/4.0/).

B.A.C. Cree / Multiple Sclerosis and Related Disorders 4 (2015) 536–545

1. Introduction Neuromyelitis optica (NMO) is a syndrome of aggressive inflammatory demyelination affecting the optic nerves, spinal cord and brain. NMO is a rare illness with an estimated population prevalence of 1:25,000–1:100,000 (Bizzoco et al., 2009; Jacob et al., 2013; Asgari et al., 2011). NMO is characterized by recurrent inflammatory attacks predominantly targeting the spinal cord and optic nerves resulting in myelitis and optic neuritis. Recovery from attacks is variable with some patients experiencing permanent or even devastating loss of function such as blindness, paralysis or respiratory failure. Although originally described as a monophasic illness, the disease course of NMO is typically relapsing, although there can be spontaneously occurring intervals of remission (Wingerchuk et al., 1999). Disability in NMO arises from cumulative relapse related injury. Recently, an autoantibody directed against the water channel aquaporin 4 (AQP4) was identified that is present in many, but not all, patients with NMO (Jarius and Wildemann, 2010). This anti-AQP4 autoantibody, also known as NMO-IgG, is pathogenic and targets atsroglial podocytes for complement mediated cell injury. Demyelination, that is well described histopathologically in NMO, is thought to be a secondary phenomenon as a consequence of the autoimmune astrocytopathy. For many years, NMO was sometimes grouped together with multiple sclerosis (MS) because both conditions can share considerable clinical overlap. However, the anti-AQP4 antibody is highly specific and helps distinguish NMO from MS. NMO treatment has focused on prevention of relapses as well as management of acute attacks. All therapeutic studies in NMO to date have been either small, retrospective case series or uncontrolled prospective studies. Controlled clinical trials in NMO have not been performed. Consequently, there are no approved treatments for NMO. Neurologists have borrowed from the experience of treating other autoimmune conditions such as systemic lupus erythematosus and myasthenia gravis and often use immunosuppressive medications “off-label”, meaning empirically based rather than indicated by the prescriber information. Immunosuppressants such as azathioprine, mycophenolate mofetil, daily prednisone, or rituximab are used with the goal of relapse prevention (Kimbrough et al., 2012). 1.1. Methodological weakness in existing NMO studies All case series in NMO using therapeutic interventions compare the frequency of relapses prior to exposure to the treatment with the frequency of relapses after treatment (Table 1). If a treatment is introduced during or following a relapse, in the immediate time following initiation of the treatment attacks will be less likely to occur. Thus a decline in relapse frequency will occur independently from treatment. This phenomenon is a form of statistical “regression to the mean” and is a common source of overestimating treatment effect sizes in open-label studies of relapsing illnesses. The unanswered question in all uncontrolled NMO studies is whether the reduction in the observed relapse frequency following treatment is greater than what would have been observed had patients not been treated. Regression to the mean is not the only potential source of confounding in the interpretation of open-label studies. Treatment selection in open-label studies is affected by both known and unknown biases introduced by both clinicians and patients. Retrospective chart reviews are also prone to various forms of recall bias and under-reporting biases. A parallel arm with either untreated, or alternately treated. patients is essential as a reference for the treated group. A well-matched study can reduce the impact of known confounders but does not control for unknown confounders, a process that necessitates randomization. Additional

537

sources of bias found in many NMO clinical studies are that they are often single-center (very few are multicenter) and have relatively small numbers of subjects. Small studies are also prone to publication bias. Single-center studies that do not find a treatment effect are unlikely to be submitted for peer-review or to be published. Thus open-label, observational studies are highly susceptible to inherent biases. As a consequence, conclusions regarding efficacy and safety from such studies could be erroneous. Because of these confounders, the optimal method for assessing therapeutic efficacy is the prospective, controlled trial with random treatment assignment that has the potential to control for these sources of bias. 1.2. The need for randomized controlled trials Although randomized controlled trials often support what is thought to be true based on observational studies, sometimes randomized-controlled trials can lead to unexpected results that challenge the prevailing thinking of the medical community. A classic example is use of hormone replacement therapy (HRT) in post-menopausal women. Multiple observational studies found benefit to HRT resulting in HRT becoming common practice. This dogma was first challenged by the heart and estrogen/progestin replacement study (HERS) that found that HRT not only failed to reduce the rate of myocardial infarctions in postmenopausal women with established coronary disease but also increased the rate of thromboembolic events and gallbladder disease (Hulley et al., 1998). The follow up study, the Women's Health Initiative, found that for HRT the overall health risks exceeded benefits among healthy postmenopausal US women (Rossouw et al., 2002). Both studies were predicated on extensive observational data supporting use of HRT from many studies involving hundreds of women (Stampfer and Colditz, 1991). Similar examples in which randomized controlled trials failed to support observational studies from the neurological literature include use of heparin for treatment of acute stroke (The International Stroke Trial, 1997), embryonic substantia nigra transplantation for Parkinson's disease (Sanders et al., 2008), mycophenolate mofetil in myasethenia gravis (Freed et al., 2001), donepezil for memory impairment in multiple sclerosis (Krupp et al., 2011) and optic nerve sheath fenestration for anterior ischemic optic neuropathy (The Ischemic Optic Neuropathy Decompression Trial Research Group, 1995). These experiences underscore the need for rigorous controlled clinical trials to prove that specific therapies are not only efficacious but also are safe. There is little question that adoption of rigorous standards for the burden of proof has profoundly transformed modern medicine for the better enhancing clinician’s abilities to provide meaningful advice to patients. Many practitioners observe that the frequency of NMO relapses decreases following the start of an immune suppressing medication. However, some NMO patients continue to experience relapses despite these treatment. These observations indicate that immune suppressant therapies are at best partially effective (if they are effective at all). Based on the experiences with other autoimmune diseases it seems likely that immune suppressing therapies would be effective in NMO. However, not all immune suppressing medications work in all autoimmune diseases. For example, although one might expect that a B cell depleting therapy (rituximab), which known to be effective in rheumatoid arthritis, would also be effective in systemic lupus erythematosus (SLE). In fact, this was not the case (Merrill et al., 2010; Rovin et al., 2012). The apparent lack of efficacy of rituximab in SLE, like that of mycophenolate mofetil in myasthenia gravis, continues to puzzle some clinicians because the trial results do not support what was accepted based on uncontrolled observational studies or personal experience. In fact it is extremely difficult to be certain of efficacy

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Table 1 Summary of studies in neuromyelitis optica immunotherapies for relapse prevention. Study

Design

Treatment

Azathioprine þ corticosteroids Mandler et al. Prospective open Methylprednisolone þprednisone þ azathioprine (1998) label Retrospective case series

Azathioprine þprednisone

Sahraian et al. (2010) Costanzi (2011)

Retrospective case series Retrospective case series Retrospective case series

Azathioprine

Kageyama et al. (2013)

Azathioprine 7prednisone Azathioprine þprednisone

1 g IV qdx5 1 mg/kg PO qdx60 from d6 2 mg/kg PO qd from d21 150 mg PO qd 5–60 mg PO qd 200 mg PO qd, 17 728 mo NR; 1–180 mo 20–80 mg PO qd 100 mg PO qd, 35–55 mo 6–10 mg PO qd

Subjects Follow up Impact on relapses

7

18 mo

7

28 mo

28

19 mo

70

22 mo

9

40 mo

103

18 mo

Elsone et al. (2014) Retrospective case series

Azathioprine prednisolone

2.5–3 mg/kg/daily 0.5– 1 mg/kg/day

Mealy and Wingerchuk (2014)

Azathioprine þprednisone

2–3 mg/kg/day 60–5 mg/ day

32

23 mo

Cyclophosphamide

0.5–1.0 g/m2 IV q4wx6

10

6 mo

Retrospective case series

Cyclophosphamide þ corticosteroids Galindo-Rodriguez Retrospective et al. (1999) case series Bichuetti et al. (2012)


Methylprednisolone þcyclophosphamide

1 g IV qdx5 0.5–0.7 g/m2 IV q4wx10

7

17 mo

Yaguchi et al. (2013)


Methylprednisolone þcyclophosphamide

1 g IV qdx3 0.5–0.75 g/ m2 IV q4wx10

4

45 mo

Cylcosporine prednisone

140–150 mg day 6– 10 mg PO qd

8

32 mo

14

Cyclosporine A þ corticosteroids Kageyama et al. Retrospective (2013) case series

IV

8.2 (6.0–9.0)4.0 (3.0–6.0) (p o0.0001) 4.7 7 2.24.7 7 2.2

IV

IV 3.5 (0–8.5)-3.5 (1.0–8.5) 3.5 (3.5–5.5)3.5 (2.0–5.5)

35% (25/70) stopped for side effects

6-5 p ¼ 0.52

46% discontinued (29 from side effects, 9 deaths, 7 ongoing disease activity, and 1 pregnancy) 53% relapsed on treatment

2.26-63 (p ¼ 0.004)

IV IV

Improved vision in 80%, 30% discontinued for severe N/V

IV

IV

IV

IV

6/7 relapsed on treatment (1 died due from relapse)

2.7-0.38 (p ¼ 0.012)

6.5-3.5 (p ¼0.30)

IV

12 mo

3 (2.0–4.0)-0 (0– 1.0) (p o 0.0001)

4.3 (1.0–8.0)3.5 (0.0–8.0) (p ¼0.0078)

1.8 7 1.60.17 0.2 1.8-0.006 (p ¼ 0.01)

Intravenous immunoglobulin Retrospective Bichuetti and de Oliveira (2013) case series Magraner et al. Retrospective (2013) case series

0.4 g/kg IV qdx5, q2m (2–10 cycles) 0.7 g/kg IV qdx3, q2m (4–21 infusions)

8

NR

8

19 mo

Methotrexateþ prednisone

50 mg IV qw, 24–72 mo 25–60 mg PO qd

7

24 mo

Methotrexate

17.5 mg IV qw, 6–28 mo

14

22 mo

Methotrexateþcorticosteroids Retrospective Minegar and case series Sheremata (2000) Kitley et al. (2013) Retrospective case series

Evidence level

IV

600 mg IV qw w1-4, 900 mg IV q2w for 48wk

IV IgG

2.18-0.64 (p o 0.0001) 1.7 (1.2–2.7)-0.47 (0.36–0.59) (p ¼ 0.028) 1.5-0 (p o 0.001)

Other effects

8.0-5.8

Eculizumab Pittock et al. (2013) Prospective open Eculizumab label

IV IgG

5.0 72.91.0 7 1.8 (p o 0.001) 0.99-0.40

Impact on EDSS

1.39 (0.19–8.0)0.18 (0–1.2) (p o 0.005)

36% improved on AI 28% VA improved in at least one eye

IV

Disease progression index 1.5-0.9

IV

3.3 7 1.32.6 7 1.5 (p ¼0.04)

IV

5.9 (5.0–7.0)4.5 (4.0–5.0)

No Gad ( þ) lesions from imaging studies

IV

5.3 (2.5–8.0)5.0 (2.5–10.0)

Disability stabilized or improved in 75%

IV


Bichuetti et al. (2010)

Regimen

Ramanathan et al. (2014)


Mycophenolate mofetil Jacob et al. (2009) Retrospective case series Sahraian et al. Retrospective (2010) case series Huh et al. (2014) Retrospective case series Retrospective Mealy and case series Wingerchuk (2014) Mitoxantrone WeinstockGuttman et al. (2006) Kim et al. (2011)

Jacob et al. (2008)

Jarius et al. (2008)

Mycophenolate mofetil

2000 mg PO qd

Mycophenolate mofetil Mycophenolate mofetil

Mitoxantrone


Mitoxantrone


Methylprednisolone þmitoxantrone

Retrospective case series Retrospective case series

29 mo

3.11-1.11 (p ¼ 0.009)

6/9 stable

33% relapsed on treatment

IV

24

28 mo

6.0 (0.0–8.0)5.5 (0.0–10.0)

21% patients stopped drug after median 16 mo

IV

1500–2000 mg PO qd

6

4 mo

1.28-0.09 (p o 0.001) 0/6 relapsed

1000–2000 mg PO qd

59

23 mo

1.5-0 (p o 0.001)

3.0-2.5 (p ¼0.005)

28

26 mo

2.61-33 (p o 0.0001)

5

24 mo

2.4 70.890.4 70.55

20

41 mo

51

48 mo

2.8 (1.0–5.7)-0.7 5.6 (1.5–9.0)(0–2.3) (po 0.001) 4.4 (1.0–7.0) (p o0.001) 1.82-0.47 5.8-4.7 (p o 0.05) (p ¼0.018)

12 mg/m2 q4wx6q12w to cumulative dose of 100 mg/m2 12 mg/m2 q4wx3q12w to cum dose of 120 mg/m2 1 g IV qdx1 12 mg/m2 q4wx3-q12wx3

IV IV 36% relapsed on treatment

4.4 7 1.92.3 7 0.7

IV

IV

Improved MRI at 12 mo

IV

IV

Natalizumab

300 mg IV Q month

5

8 mo

3.2 (3.0–4.0)-1.4 (1.0–3.0)

4.0 (1.0–7.5)5.8 (1.5–9.0)

IV

Rituximab

375 mg/m2 IV qwx4,q6– 9m 375 mg/m2 IV qwx4,q6– 9m

8

12 mo

2.6-0 (p ¼0.008)

IV

25

19 mo

1.7 (0.5–5.0)-0.0 (0.0–3.2) (p o 0.001)

7.5-5.5 (p ¼0.013) 7.0 (3.0–9.5)5.0 (3.0–10.0) (p ¼0.02)

4

NR

10

NR

30

24 mo

2.3 (1.55–2.79)0.51 (0.46–1.04) 2.4 (1.0–5.0)0.93 (0.0–7.5) 2.4 (0.4–8.0)-0.3 (0.0–4.0) (p o 0.001)

23

32 mo

18

24 mo

7

Rituximab

Rituximab

Bedi et al. (2011)


Methylprednisolone þrituximab

Bomprezzi et al. (2011)


Ip et al. (2013)


Lindsey et al. (2012)


Gredler et al. (2013)


Rituximab

Yang et al. (2013)


Rituximab

Rituximab Rituximab

375 mg/m2 IV qwx4,q6– 9m 1g IV biweekly x2 q6– 9m 375 mg/m2 IV qwx4, repeat when CD27þ 40.05% PBMCs

Infections reported in 20%, deaths due to septicemia (1) and brainstem relapse (1)

IV

IV 5.3 (1.5–8.5)5.0 (1.5–8.0) 4.4 (1.0–8.5)3.0 (1.0–7.5) (p o0.001)

IV Infections in 40% of patients but no serious infections (21/30 relapse free) Disease improved or stabilized in all patients

IV

53% (8/15) relapse free at 4 2% B-cells

IV

IV

1.87 (0.31–5.14)0.0 (0.0–1.33) (p o 0.01) 1.17-0.06

7.0 (3.0–9.0)5.5 (0.0–8.0) (p o0.02)

24 mo

2 (1–4)-0 (5/7 relapse free over 24 mo)

8.0 (6.9–9.5)7.0 (3.0–9.5)

IV

8

NR

3.7 (0.0–8.0)4.8 (2.0–10.0)

IV

375 mg/m2 IV q2–6 m x3–16

4

10–78 mo

5.3 (3.0–7.5)3.3 (1.0–7.5)

IV

100 mg IV qwx3, repeat when CD27þ 41% PBMCs

5

12 mo

4 of 5 pts treated within 6 mo of onset relapsed 2.8 (2.25–3.0)0.4 (0.0–0.83) (p o 0.05) 1.16 (0.4–2.6)-0.0 (0.0–0.0)

5.5 (3.0–8.0)5.0 (2.5–8.0)

No new T2 lesions and no IV Gad( þ ) on MRI

1 g IV qdx10 (acute attacks) 1 g IV biweekly q6 m Methylprednisolone 7plasma exchangeþrituximab 1 g IV qdx5 (acute attacks) 1.4 vol qdx5 (acute attacks) 1 g IV q2w x2, repeat when CD27þ 41% PBMCs Methylprednisolone þimmunoglobulin þrituximab 0.5–1 g IV qd, d1–5 (acute) 0.4 g/kg IV qd d510 1 g IV biweekly q6– 9m Rituximab 375 mg/m2 IV qwx4, repeated at MD discretion

539

Retrospective case series Retrospective case series Retrospective case series

Pellkofer et al. (2011) Kim et al. (2011)

9

Mycophenolate mofetil


Natalizumab Kleiter et al. (2012) Retrospective case series Rituximab Cree et al. (2005)

7.5–17.5 mg QW 605 mg daily


Cabre et al. (2013)

Methotrexateþ prednisone

5.1-4.1 (p o0.01) 12 mo 7 8 mg/kg IV Q month Tocilizumab Retrospective case series

This table summarizes the available literature on therapies that are used as preventive medications for NMO relapses. Nearly all studies are retrospective, uncontrolled case series. Only two studies used prospective data and both of which were open-label and uncontrolled. The medication, treatment regimen, number of subjects and duration of post-treatment follow up are listed along with the proposed effect on relapses and, when available, effect on disability as measured by the EDSS. All studies are class IV studies according to the evidence based guidelines of the AAN (O'Connor et al., 2009). Abbreviations: mo¼ month; NR ¼not reported; N/V¼ nausea and vomiting; AI¼ ambulation index, VA ¼visual acuity; Gad( þ) ¼ gadolinium DPTA enhancing lesion.

Reduction in pain and fatigue 2.9-0.4 (p o 0.005)

IV

17% relapsed on treatment 2.89-0.33 (p ¼ 0.004) 20 mo 30 1 g IV biweekly x2 q6– 9m RItuximab Retrospective case series

Mealy and Wingerchuk (2014) Tocilizumab Araki et al. (2014)

Table 1 (continued )

Treatment Design Study

Regimen

Subjects Follow up Impact on relapses

Impact on EDSS

Other effects

IV


Evidence level

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based on purely observational data because of the potential for confounding and systematic biases. Given that there are no controlled trials in NMO, it seems that there is a significant unmet need for well-designed clinical trials in NMO that will lead to proved, effective and reasonably safe treatments. The most direct method to prove efficacy is to compare an active treatment vs. no treatment or placebo control. The use of placebo has two functions. First, the active treatment is compared against the natural history of the illness (no treatment). Second, placebo use helps maintain uncertainty of both investigators and study participants with respect to treatment allocation. Investigators that know about treatment assignment are systematically prone to favor active treatment (Noseworthy et al., 1994). Similarly, study subjects who are aware of treatment assignment may under report symptoms. Thus knowledge of treatment assignment can bias studies leading to false positive conclusions (type1 errors). There is little doubt that a placebo controlled NMO trial could provide proof of efficacy. However, because of the devastating nature of the disease some clinicians are reluctant to expose potential study patients to the risk of no treatment associated with placebo. Some clinicians believe that the available observational data is sufficiently convincing that placebo should not be used and instead recommend that NMO studies either use an active comparator or add-on (combination) study design. 1.3. The case for no treatment Although the concepts thus far outlined make a scientific case for use of placebo the question remains as to whether a placebo controlled trial in NMO is ethical. Although there is a relationship between scientific rigor and ethical trial conduct the two concerns may not always be harmonious. Disease specific aspects of NMO present unique ethical challenges that must be carefully considered before proceeding with clinical trials. First, the severity of the condition and the potential for disability or even death from NMO relapses must be consciously weighed in contemplating use of placebo. Second, NMO is a rare disease with a relatively small potential population to study. Any clinic trials undertaken must have the potential to fully recruit study subjects in order to answer the question regarding therapeutic efficacy. Third, there is lack of evidence regarding the effects of the current treatments used empirically for NMO relapse prevention. Lastly, there is disagreement within the clinical and scientific community as to whether a placebo arm in NMO clinical trials is acceptable. Fortunately, much work has already been completed in understanding the circumstances when placebo-controlled trials can be undertaken (Freedman, 1990). There are five accepted contexts in which placebo control is ethical: (a) when there is no standard therapy, (b) when standard therapy is no better than placebo, (c) when there is doubt regarding the net therapeutic advantage of standard therapy, (d) when standard therapy is not available and (e) when standard therapy is no treatment. Crucial to answering the question regarding whether a placebo-controlled trial in NMO is ethical is the understanding as to the meaning of “standard therapy” (http://www.wma.net/en/30publications/10policies/b3/). Should standard therapy be defined as any intervention that is used by physicians empirically regardless of the evidence supporting the intervention's use or does the term “standard” require a scientific rationale? 1.4. “Standard of care” for NMO The concept of “standard of care” is generally understood to mean that there is a diagnostic study or treatment that a clinician should use for a certain type of patient. “Standard of care” also has certain legal ramifications because it is defined as the way in


which the average, qualified provider in a community would practice. Although perhaps not absolutely defined, there are two important concepts that underlie the notion of standard of care. First is the principal that there are treatments or tests that physicians should use, implying that there is a compelling basis for these interventions and, furthermore, that not administering these interventions would be harmful. Second, the community of similar practitioners must be generally knowledgeable about the intervention. Thus, there are standards of care for treatments that are clearly proven to be beneficial and are generally known to providers. Interventions that are not proved to be beneficial are considered experimental and therefore are not part of the standard of care. The terms “proven” and “high level of evidence” are commonly used in discussions related to standards of care and publications of clinical guidelines to treat diseases. Over the last few decades substantial progress has been made to use medical treatments in accordance with the principles of “evidence based medicine,” that is, to base clinical treatments on high-level evidence (Sackett et al., 1996). When the American Academy of Neurology evidence based guidelines are applied to NMO therapeutic studies, all current treatments used to prevent NMO relapses are considered class IV studies (uncontrolled studies and therefore having the lowest level of evidence). It is likely that, were the therapeutics and technology subcommittee of AAN to classify these interventions for NMO, they would receive a “U” designation meaning unknown or unproven based on data that is either “inadequate” or “conflicting” (Gross, 2009). As such, none of the current empirically used NMO therapies meet the criteria for establishing clinical guidelines and probably should not be referred to as “standard of care.” The European Federation of Neurological Societies' (EFNS) recognizes that current guidelines for NMO treatment are based only on class IV evidence (Sellner et al., 2010) as are other clinical guidelines (Kimbrough et al., 2012). Until studies are conducted in NMO that yield proved therapies, current treatments for relapse prevention in NMO perhaps should be referred to as available, empiric, unproven therapies rather than being labeled as “standard of care”. That there is no clear “standard of care” does not mean that physicians should not treat NMO patients with currently available medications. Physicians remain free to prescribe unproved medications and treat their patients based on the limited available data as long as their patients understand that these treatments are unproven and carry risk. These issues are not unique to NMO and the phrase “standard of care” is often misused in medicine to support day-to-day clinical decisions that are not evidence based (Strauss and Meirion Thomas, 2009).

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equipoise that is the crux of the debate about placebo controlled NMO trials: is a placebo-controlled arm consistent with competent medical care? This question can be addressed by evaluating the adequacy of the evidence of available therapies and a clear understanding of not only their potential benefits but also their risks. For example, if a hypothetically available therapy of unproven benefit carried absolutely no risk to the study subjects, withholding such a therapy would be hard to justify. However, in the actual case of NMO, all currently available empirically used therapies carry real risks for study subjects. The most commonly used empiric treatments for NMO are azathioprine, mycophenolate mofetil and rituximab. Each of these treatments has a “boxed” warning indicating that severe adverse events are known to be treatment associated. Azathioprine treatment carries the risks of serious opportunistic infections including progressive multifocal leukoencephalopathy (PML), lymphoma, hepatosplenic T-cell lymphoma and Sweet's syndrome (acute febrile neurotphilic dermatosis) et al., 2014b. Mycophenolate mofetil carries the risks of polyomavirus associated nephropathy (PVAN), PML, cytomegalovirus (CMV) infections, reactivation of hepatitis B or C, lymphoproliferative disease and lymphoma (http://www.accessdata.fda.gov/drugsatfda_docs/label/2009/ 050722s021,050723s019,050758s019,050759s024lbl.pdf). Rituximab carries the risks of severe or even fatal infusion reactions, PML, hepatitis B reactivation and fulminant hepatitis and severe mucocutaneous reactions (http://www.accessdata.fda.gov/drugsatfda_docs/label/2010/103705s5311lbl.pdf). Therefore none of the existent empiric therapies are sufficiently safe to justify use in all circumstances. Because each of these treatments carries bona fide risks to study participants none of these treatments are necessarily better than no treatment. It is precisely because no currently available treatment has proven benefit, and because all therapies are known to potentially cause harm, that the risk to benefit ratio for an active comparator arm may be less acceptable to that of a placebo-controlled arm. Because of the issue of known potential harm from unproven therapies, some might even argue that use of unproven active comparators either alone or in the setting of addon studies poses an even greater ethical challenge than use of placebo-control. Once any treatment is proved to be efficacious, and to have a favorable risk to benefit ratio, then that treatment could be used as an active comparator against which newer treatments could be measured. Failure to adequately account for actual risks of unproven therapies, and acceptance of uncontrolled data as adequate evidence of efficacy, may account for why some clinicians are strongly opposed to use of placebo-control in NMO trials.

1.5. Is there clinical equipoise? 1.6. The case for and against active comparators The primary ethical concern in the case of placebo-control in NMO clinical trials rests on the relative merits of answering the scientific question regarding efficacy when compared to the relative risk of harm to which those patients in the placebo-control group will be exposed. These concerns are the underpinning of the concept of clinical equipoise that many consider to be one of the determining principals as to whether a clinical trial should or should not be conducted. Clinical equipoise, or counterbalance, refers to the concept that there is genuine uncertainty in the expert medical community over whether a treatment will be beneficial (Freedman, 1987). Clinical equipoise involves two requirements. The first has to do with uncertainty regarding the relative scientific and clinical merits of each treatment arm. The second requires that each treatment arm be consistent with competent medical care. In the case of NMO, uncertainty regarding the efficacy of any treatment exists because sufficiently rigorous studies have never been conducted. It is the second point in clinical

Head-to-head clinical trials are typically designed to demonstrate that one drug is superior to another drug. Although blinding can be accomplished in active comparator studies, efficacy is evaluated only by differences between the active treatments. Relative efficacy vs. the natural history of the disease in the population under study cannot be evaluated because there is no untreated reference group. Several clinical trials in MS successfully demonstrated that one treatment is superior to another (Cohen et al., 2010; Coles et al., 2012). In these trials, head-to-head study designs used a reference treatment that is already known to be efficacious based on prior placebo-controlled studies (Mikol et al., 2008; O'Connor et al., 2009). In NMO, the concern about a headto-head study for proof of efficacy is that there are no treatments that are proven efficacious. In theory, if one treatment were actually harmful, then a treatment that has no benefit might appear to be efficacious when compared to a treatment that is harmful.

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In NMO, a retrospective study that compared treatment of interferon-β to immune suppressant medications (primarily azathioprine and mitoxantrone) found that the immune suppressant treated patients were less likely to relapse compared to the interferon-β treated patients. The authors concluded that immune suppressant treatments were superior to interferon-β for prevention of NMO relapses (Papeix et al., 2007). This conclusion is predicated on the assumption that treatment with interferon-β did not hasten NMO relapses. If interferon-β triggered NMO attacks, then the difference between the two groups could be entirely explained by interferon-β causing harm rather than due to a beneficial effect of immune suppressants. Without a natural history (no treatment control), it is impossible to accurately evaluate relative efficacy of these treatments. In fact, several studies have suggested that interferon beta might trigger NMO relapses (Warabi et al., 2007; Shimizu et al., 2010). Thus to understand the difference between these two treatment groups a third arm of untreated patients would have been necessary. Without this untreated arm, it is impossible to determine whether the difference between immune suppressant and interferon-β was due to benefit from the immune suppressants or harm caused by interferon-β. Because empiric NMO treatments are unproven, some regulatory agencies are skeptical of head-to-head or add-on NMO study designs using unproved active comparators. The concern is that if a difference between the new treatment and the unproved active comparator is found, and this difference is caused by harm of the active comparator, then approval of the new treatment might not be due to a benefit from the new treatment but rather be caused by harm inflicted by the active comparator. The cardiac arrhythmia suppression trial (CAST) is an excellent example of how important the inclusion of a placebo group can be in head-to-head studies (Echt et al., 1991). This study compared flecainide and encainide to placebo to test the hypothesis that suppression of ventricular ectopy with these medications can reduce the incidence of sudden death after a myocardial infarction. This study showed that both flecainide and encainide were associated with excess mortality relative to placebo. If a placebo group had not been included then one might have concluded that flecainide was superior to encainide because there were more cardiac deaths in the encainide group when, in fact, neither treatment was beneficial. 1.7. Combination therapy or add-on studies One proposed strategy to mitigate the risk of placebo exposure in NMO clinical trials is the so-called add-on study design. In this trial design, a novel therapy vs. placebo is added to an existing therapy to test the hypothesis as to whether the combination of the new therapy plus the existent therapy is superior to the existent therapy alone. An example of such a study design from MS is study of natalizumab in combination with interferon beta-1a IM (Rudick et al., 2006). An important limitation to this study design is that one does not know how the new medication would have performed independently from the combination. In the case of natalizumab, the combination was superior to interferon beta-1a IM but it remains unknown whether the combination is better than natalizumab alone. In order to show that a combination treatment is beneficial, a third treatment arm is needed in order to compare each treatment against each other as well as against the combination. An example from MS is the CombiRx trial of interferon beta-1a IM and glatiramer acetate (Lublin et al., 2013). In this study, had a glatiramer acetate only arm not been included in the study design, one would have erroneously interpreted that the combination of interferon beta-1a IM with glatiramer acetate was superior to interferon beta-1a IM. This study illustrates the importance of including correct controls arms for combination studies.

1.8. The moral hazard of non-participation Clinical equipoise does not oblige individual clinicians to participate in trials. Clinicians who prefer to treat patients empirically will continue to do so. However, in so choosing those clinicians will not contribute to the overall advancement of the state of understanding of NMO. Such decisions represent missed opportunities to advance NMO therapeutic knowledge. It is the goal of current NMO clinical trials to develop therapies that are of proved benefit. Proof of benefit will lead to regulatory approval and subsequently acceptance by payers resulting in broad therapeutic availability. Without these key steps, NMO patients may not have access to new treatments and will continue to not know whether the therapies that they may be currently taking have risk to benefit profiles that favor use. Although NMO is a rare disease, as many as 3000–6000 persons in the United States could be affected. Global estimates of the prevalence of NMO could be as high as 140,000 individual. It is essential that clinicians who chose to not enroll their patients in NMO clinical trials understand that that they are voluntarily slowing progress towards developing proved NMO therapies and that non-participation has global ramifications. 1.9. Will NMO clinical trials harm patients? In general, the risk of harm should be minimized for all trial participants. That being said, no study can minimize all risks to all subjects. Every study design requires the occurrence of clinically relevant events. In the case of NMO, if one is seeking to prove that a treatment has an impact on relapses then one must show that there is a statistically significant difference in the occurrence of relapses between two or more treatment arms (at least in a superiority study design). To do this, relapses have to occur. The same applies to all clinical trials in all disease states. Without the occurrence of medically relevant events there is no way to distinguish between treatment arms. Given that clinically relevant events are required, and that one has an ethical obligation to minimize harm, then it is logical that studies should be designed to require the lowest number of medically relevant events in order to adequately answer the primary scientific question. In the case of NMO, if two clinical trial designs with the same medication were compared, then the study design that requires fewer relapses in order to determine efficacy would be ethically preferable to a study that requires a greater number of relapses. If one assumes that an active comparator has efficacy and one compares a new therapy to the active comparator, then the number of medically relevant events in order to detect a difference between the two treatment arms will be greater than if one compares the new treatment to placebo (Table 2). This is another reason why placebo-controlled trials are preferable to active comparator studies. Placebo controlled studies expose the population under study to less harm because these studies require fewer medically relevant events than with an active comparator design. 1.10. Does disease severity or rarity matter with respect to placebo control? The rarity and the severity of NMO matter to research ethics. If a condition is rare, we may want to better protect those who suffer from it. At the same time there is a societal obligation to conduct research on rare conditions so that those afflicted do not suffer from a lack of research. Similar concerns also apply to the case of severity: patients with severe conditions have a greater burden; however, this burden also makes research all that more important. NMOs rarity and severity heighten the stakes for patients and clinicians resulting in potentially greater polarization of opinion. This polarization makes the process of evaluating


Table 2 Sample size calculations for placebo-controlled and active comparator studies. 1:1 Randomization Events PBO vs. drug A (60% effective) PBO vs. drug B (50% effective) PBO vs. drug C (40% effective) Drug A (60% effective) vs. drug C (40% effective) Drug B (50% effective) vs. drug C (40% effective)

28 (20/8, PBO/A) 42 (28/14, PBO/B) 67 (42/25, PBO/C) 167 (67/100, A/C) 732 (333/ 399, B/C)

1:2 Randomization

Subjects Events 50 70 104 416 1664

27 (15/12, PBO/A) 42 (21/21, PBO/B) 69 (31/38, PBO/C) 174 (100/74, A/C) 797 (498/ 299, B/C)

Subjects 57 78 117 465 1869

This table shows the number of events and the number of subjects needed for a one-year duration NMO clinical trial with the following assumptions: the event rate for the untreated group is assumed to be 0.8 (80% of untreated subjects are expected to relapse), α ¼0.05 and β¼ 0.90. The first three rows show the number of events and subjects needed for drugs A, B and C that have decreasing efficacy on relapse prevention. The second set of three rows show the number of events and subjects needed comparing these drugs A or B to drug D that is less effective. The table also shows the modest impact of unequal treatment allocation on the number of events and subjects needed. These sample size calculations not only show that a greater number of events are needed for active comparator compared to placebo control studies but also can be used to evaluate relapse related injury. Some clinicians believe that NMO relapses on treatment are less severe than relapses on no treatment. This presumption has been used to argue in favor of active comparator rather than placebo studies. Although relapse severity in treated vs. untreated NMO patients has not been rigorously investigated, the percentage of reduction in relapse severity resulting in parity between placebo controlled and active comparator studies can be calculated using event rates. Taking the example from a placebo controlled trial with a medication that is 60% effective (Drug A) and comparing this to the events required for an active comparator study of two drugs that are 60% (Drug A) and 40% (Drug C) effective respectively, relapses in the actively treated patients would need to be 87% less harmful compared to the severity of relapses that occur in 20 placebo treated patients. Although minor or trivial relapses may very well occur in NMO in treated patients, it seems unlikely that the average relapse in a treated patient will cause only 13% or less of the harm of relapses in untreated patients. Therefore, placebo controlled studies not only require fewer subjects and medically relevant events but are also associated with overall less event related harm to the study subjects than active comparator trials.

and judging as to how to proceed require even greater consideration than possibly less contentious clinical circumstances. Consideration of the issues in NMO clinical trials requires inclusiveness of all stakeholders, openness, and respect for independence of opinion. Ultimately, the choice comes down to the patient and the provider. There is little question that placebo-control studies in NMO can be conducted ethically. If the relevant uncertainties regarding current treatments and potential scientific and clinical values of the study are adequately explained there is no reason to think that potential study participants would not be able to provide informed consent. Clinical trials in NMO must appeal to the sensibilities of both investigators and study subjects in order for adequate subject recruitment and to maintain interest in participation. The challenge for clinical trials in NMO will be recruitment due to the relative scarcity of study subjects and the availability of empiric treatments. Successful study designs must target the population under study and create sufficient safeguards to insure patient safety as best as is possible while at the same time encouraging subject participation and having a sufficiently rigorous design so that the results are readily interpretable. 1.11. Study design considerations in placebo controlled NMO trials If one accepts the arguments for placebo control in NMO trials then strategies to reduce exposure to placebo while at the same

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time having the potential to provide robust evidence of efficacy are needed. Several design considerations include limiting the duration of placebo exposure, unequal treatment allocation, time to event design, event based sample sizes (rather than subject number), provisions of rescue therapy, provision of rescue therapy for relapse treatment, an un-blinded data safety monitoring committee and the possibility of open-label extension with active treatment. Ideally these studies should also receive approval from regulatory agencies so that no study moves forward without the potential for use in product registration. The unique safety profile of each product should be taken into consideration for each study design especially with respect to prior treatments that could have prolonged immunological effects. Additional challenges include development of disease specific endpoints especially for NMO relapses that can be distinct from those of MS. Clear definitions of the population under study are also necessary with respect to both seropositive NMOSD and seronegative NMO subjects. It is hoped that well designed studies will be able to recruit sufficient numbers of NMO subjects during a reasonable time interval to provide evidence for therapeutic efficacy of at least one treatment. Future studies could build upon the successful indication of a proved NMO disease modifying therapy and use head-to-head superiority designs that will not be complicated by use of placebo.

Conclusions The field of NMO research is at a remarkable crossroads. In recent years major advancements in understanding the clinical spectrum and the pathoetiology of NMO were made. Some available treatments appear to have benefit and several new therapies are being investigated as treatments for NMO in randomized, controlled trials. Returning to the five recognized contexts in which placebo control is considered ethical, placebo controlled trials in NMO can be justified based on (a) the absence of a standard therapy, (b) uncertainty as to whether current therapies are better than no treatment, (c) existing doubt as to whether there is a net therapeutic advantage of existing therapies relative to their risks. In addition, although not discussed in detail in this article, some existent therapies, such as rituximab, may not be generally available due to payer restrictions. Constructive debate regarding whether NMO clinical trials should or should not use a placebo control arm has occurred. The logic of clinical purpose indicates that placebo control in NMO is ethical because the currently used empiric therapies carry real risks and are without proven benefit. A major challenge for those involved in NMO clinical trials studies include optimization of study design to reduce the risk of placebo exposure as much as possible while at the same time yielding results that are readily interpretable. The scarcity of the disease will also necessitate global outreach involving multiple centers with active recruitment strategies. Whether any of these studies will successfully recruit a sufficient sample of NMO subjects remains to be determined. Moreover, the NMO community should be prepared for the possibility that the first controlled studies in NMO may not be successful. This was the case for MS therapies in part because of limitations in study design and inclusion criteria. Only through the iterative learning process was sufficient progress made in MS that lead to the first proven therapy in 1993 (interferon beta-1b). Subsequently, 11 other medications have now been approved. Hopefully, the pathway to proof of efficacy in NMO will have benefited from the experience in MS and be successful from the start.

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