When should researchers cite study differences in response to a failure to replicate?

Abstract

Scientists often respond to failures to replicate by citing differences between the experimental components of an original study and those of its attempted replication. In this paper, we investigate these purported mismatch explanations. We assess a body of failures to replicate in neuroscience studies on spinal cord injury. We argue that a defensible mismatch explanation is one where (1) a mismatch of components is a difference maker for a mismatch of outcomes, and (2) the components are relevantly different in the follow-up study, given the scope of the original study. With this account, we argue that not all differences between studies are meaningful, even if they are difference makers. As our examples show, focusing only on these differences results in disregarding the representativeness of the original experiment’s components and the scope of its outcomes, undercutting other epistemic aims, such as translation, in the process.

Full text

Vol.:(0123456789)
Biology & Philosophy (2022) 37:39
https://doi.org/10.1007/s10539-022-09873-y
1 3
When should researchers cite study differences inresponse
toafailure toreplicate?
DavidColaço1· JohnBickle2,5· BradleyWalters3,4
Received: 12 April 2022 / Accepted: 14 August 2022 / Published online: 2 September 2022
© The Author(s) 2022
Abstract
Scientists often respond to failures to replicate by citing differences between the
experimental components of an original study and those of its attempted replication.
In this paper, we investigate these purported mismatch explanations. We assess a
body of failures to replicate in neuroscience studies on spinal cord injury. We argue
that a defensible mismatch explanation is one where (1) a mismatch of components
is a difference maker for a mismatch of outcomes, and (2) the components are rel-
evantly different in the follow-up study, given the scope of the original study. With
this account, we argue that not all differences between studies are meaningful, even
if they are difference makers. As our examples show, focusing only on these dif-
ferences results in disregarding the representativeness of the original experiment’s
components and the scope of its outcomes, undercutting other epistemic aims, such
as translation, in the process.
Keywords Replication· Translation· Model organisms· Experiment· Neuroscience
* David Colaço
djc60@pitt.edu
John Bickle
jbickle@philrel.msstate.edu
Bradley Walters
bwalters2@umc.edu
1 Munich Center forMathematical Philosophy, LMU Munich, Munich, Germany
2 Department ofPhilosophy andReligion, Mississippi State University, Starkville, USA
3 Department ofNeurobiology andAnatomical Sciences, University ofMississippi Medical
Center, Jackson, USA
4 Department ofOtolaryngology andCommunicative Sciences, University ofMississippi Medical
Center, Jackson, USA
5 Department ofAdvanced Biomedical Education, University ofMississippi Medical Center,
Jackson, USA
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D.Colaço et al.
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39 Page 2 of 17
Introduction
A “crisis” in medicine (Ioannidis 2005) and psychology (Open Science Collabo-
ration 2015) has brought with it an increased scrutiny of the role of replication
in science. This scrutiny includes debates about the relative importance of rep-
lication over other epistemic practices (Feest 2019), the social mechanisms that
promote replication (Romero 2018), and even the meaning of ‘replication’ itself
(Machery 2020).
Failures to achieve epistemic aims fuel worries about replication in scientific
fields beyond medicine and psychology. For instance, a program called “Facili-
ties of Research Excellence—Spinal Cord Injury” (FORE-SCI), established by
the National Institute of Neurological Disorders and Stroke (NINDS), began after
perceived failures to translate results in animal studies of spinal cord injury to
therapeutic interventions in human patients. Researchers designed FORE-SCI to
replicate several notable spinal cord injury studies (Steward etal. 2012a). This
program ended up with a “surprising preponderance of failures to replicate,” and
researchers proposed 11 “reasons for a failure to replicate” (Steward etal. 2012a,
p. 601).
While these neuroscientists clearly value replication, their 11 reasons for these
failures mostly address differences between the experimental components of the
original study and its attempted replication. While concerns over the requisite
degree of “exactness” or “directness” for replications are common in recent lit-
erature (Schmidt 2009; Zwaan etal. 2018; Feest 2019; Romero 2019), and study
differences are often noted by practicing scientists, there remains a question that
has received little explicit discussion: under what circumstances should research-
ers rest content with a mismatch explanation for reported failures to replicate?
In this paper, we account for mismatch explanations. A mismatch explanation
is one where (1) the match of experimental components is a difference maker
for the match of experimental outcomes, and (2) the components are relevantly
different in the follow-up study, given the scope of the original study. With our
account, we argue that not all differences between studies are candidates for mis-
match explanations, even if they are difference makers. As examples from the
FORE-SCI program show, addressing study differences without consideration of
the original study’s scope can undercut other epistemic aims, such as translation.
Thus, our aim in this paper is not to deny that mismatch explanations are ever
defensible. We think that they are. Rather, we question whether cases like some
of those reflected in FORE-SCI meet both conditions for defensible mismatch
explanations.
In “SectionMismatch explanations”, we give an account of mismatch expla-
nations. In “Section Attempted spinal cord injury replications”, we discuss
the FORE-SCI research program, in which scientists cite study differences in
response to several reported replication failures in spinal cord injury research. In
“SectionAssessing a purported mismatch explanation”, we discuss a FORE-SCI
case in more detail and assess whether a mismatch explanation is appropriate. In
Section “Why some study differences don’t matter for replication”, we address
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the consequences of explaining replication failures solely in terms of difference
makers, including the effects of these explanations on other epistemic aims. We
also propose a method for resolving inappropriate appeals to mismatch explana-
tions in the future. We conclude by speculating that mismatch explanations are
popular for several reasons, including researchers’ concerns about culpability.
Mismatch explanations
The term ‘replication’ is used in a variety of ways within and between scientific dis-
ciplines. In some cases, it is synonymous with reproducing an earlier outcome, and
it is often equated to producing robust supportive evidence or extrapolating scien-
tific results (Schmidt 2009). Debates about what we want from a replication also are
common. These debates result in part from the fact that studies will invariably differ
in some manner (Feest 2019; Romero 2019). Thus, there will always be differences
between an original study and its follow-up.
Given that differences between studies are inevitable, when is it appropriate to
explain reported replication failures in terms of these differences? In answering this
question, we do not identify some novel kind of explanation. Instead, we account
for when a mismatch serves as an appropriate probe into whether a follow-up study
counts as a bona fide replication attempt and thus has epistemic consequences. We
present two conditions for a defensible mismatch explanation. The first condition
is that any cited difference between two studies’ components must be a reason the
two studies have different outcomes. We call this the difference maker condition.
Whether a mismatch meets this condition is determined by manipulating the match
of the components and measuring the match of the outcomes. For this reason, our
account satisfies an interventionist account of causal explanation (Woodward 2005).
This condition captures the fact that differences alone are not enough. They must be
difference makers.
The difference maker condition alone does not capture everything of importance
for a mismatch explanation. To understand why, we address the nature of experi-
mental components and outcomes of a study. First, how do we construe experi-
mental components and their representativeness? To match an original study in a
replication, we must hold some components constant. These are what Machery’s
resampling account of replication calls fixed factors (2020). Take a study that tests
the specific effect of ibuprofen on symptom severity when used in COVID-19
patients. If this drug is substituted with acetaminophen in a follow-up trial, this new
study does not follow the original. The two drugs and how they interact with the
SARS-CoV-2 virus and its receptors differ (Gonzalez-Paz etal. 2020). By contrast,
there are what the resampling account calls random factors. Take a study that tests
the effect of opioids for pain management in cancer patients. As the mechanism of
action across several different opioid medications is expected to be similar for pain
relief, the test of any single opioid medication might be considered representative of
other opioids. In this case, replicators need not use (say) oxycodone if it was used
in the original study. In this study, oxycodone stands for the population of opioids.
However, the replicators cannot substitute just any drug in the follow-up trial. They
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D.Colaço et al.
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must use an opioid. Random factors need not be held constant but must be cho-
sen from some population to which they are representative. The character of this
population is dependent upon the scope of the experimental outcome and stated con-
clusions. In other words, the original researchers’ intended scope of their findings
should inform which populations are representative for random factors. Replicators
must match a factor’s representativeness when attempting to replicate a study.1
Second, how do we construe experimental outcomes and their scope? In how
general of terms are the scientific outcomes to be described by researchers (Simons
etal. 2017; Nosek and Errington 2020)? Some degree of generality beyond the spe-
cifics of an individual experiment is expected if outcomes apply to something more
general than the sample of individuals or specific conditions studied in any single
experiment. For instance, rodent research that is intended to translate to therapeutic
interventions in humans must have outcomes whose scope applies to humans, or at
least to more than just the cohort of mice or rats tested in an individual study. The
scope of these outcomes relates to the representativeness of the components.
Considering representativeness and scope, the second condition for a mismatch
explanation is that a difference must count as a relevant mismatch. We call this the
relevance condition. When are mismatches relevant? First, fixed factors can be mis-
matched. For instance, the original researchers or replicators might inadvertently
introduce a component into their study that results in a confound, or a factor that is
distinct from, but covaries with, the hypothesized effect (Schickore 2019).2 Second,
random factors can be mismatched. This occurs when a component in the follow-
up is not representative of random factors in the original study, given the original
study’s scope. This condition captures that not all differences matter for replication,
even if they are difference makers. Returning to the opioid example, using hydroco-
done instead of oxycodone is not a relevant mismatch if oxycodone was intended to
be representative of any opioid. Using a drug that is not an opioid in this example,
however, is not representative, so this would be a relevant mismatch.3
For the purposes of this paper, we follow the resampling account and take rep-
lication to establish reliability: when fixed factors are held constant, testing repre-
sentative random factors should result in the same outcome with a high frequency
(Machery 2020). If fixed factors are not held constant or the random factors of the
follow-up are not representative, then the follow-up is not a replication attempt. This
requirement of the resampling account captures one reason mismatch explanations
can be valuable. A follow-up study cannot satisfy both the relevance condition and
the resampling account. Returning to the example, either hydrocodone is representa-
tive of the opioid population and its use in a follow-up should count as a replica-
tion attempt, or it is a relevant difference, and its use in a follow-up study should
1 This is not to say that original researchers’ intentions are necessarily the best way in which the study in
question could be performed. What matters in replication, and what distinguishes it from a mere follow-
up, is that the replication attempt fits the fixed and random factors of the original study.
2 This need not be inadvertent. For instance, replicators might not include a component if the original
report does not state it explicitly (Hensel 2020).
3 Our account thus supplies a more precise basis to assess mismatch explanations than stating that “criti-
cal features” must be duplicated in a replication (Zwaan etal. 2018, p. 6; Romero 2019).
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not count as a replication attempt. A mismatch explanation that meets the relevance
condition entails that the follow-up study does not count as a replication failure.
More importantly, a mismatch explanation pinpoints a plausible cause for the differ-
ence in outcomes that does not call the reliability of the original study into question.
Attempted spinal cord injury replications
Given the debilitating consequences of human spinal cord injuries, researchers
induce spinal trauma in animal models to learn how to “reduce secondary injury,
improve recovery, or enhance axon regeneration” in hopes that they can extend this
knowledge to humans (Steward etal. 2012a, p. 597). In 2003, NINDS developed a
program, FORE-SCI, to promote and fund replications of several notable studies in
this area of research. FORE-SCI was motivated by a perceived lack of therapeutic
interventions in humans, despite “apparent progress,” or reports of successful origi-
nal studies in animal models (Steward etal. 2012a, p. 597). This lack of translation
also raised concerns about the reliability of this research that was rarely, if ever, rep-
licated prior to FORE-SCI.
In hindsight, these concerns were well-founded. In FORE-SCI, there were a “sur-
prising preponderance of failures to replicate” spinal cord injury studies (Steward
etal. 2012a, p. 601). Of 12 reported replication attempts from FORE-SCI, six were
“no replication,” two were “partial replication,” one was “mixed results,” one was
inconclusive, and two were successful (Steward etal. 2012a, p. 600). If these out-
comes were not troubling enough, one successful replication resulted in a lower
effect compared to the original study, and the other was only “replicated” following
a discovery of a mismatch resulting from a previously unqualified component of the
original study (more on this example in Sect.4). While not a systematic attempt to
replicate studies in a field (unlike, e.g., Open Science Collaboration 2015), these
outcomes are troubling for spinal cord injury research. On an optimistic interpreta-
tion, half of the chosen studies failed to replicate. On a pessimistic interpretation, all
attempts involved some complications in replicating the original study.
Closer inspection of one failure to replicate from FORE-SCI is insightful.
Researchers set out to replicate a study designed to test the effect of inosine on trans-
midline axons in the rat corticospinal tract (Benowitz etal. 1999). Inosine is a purine
nucleoside, which can affect a neuron’s axonal growth invitro. In the original study,
inosine injection was reported to cause pyramidal cells to grow and sprout their
axons into denervated spinal white matter, suggesting that inosine intervention may
be an effective means to “restore essential circuitry after injury to the central nerv-
ous system” (Benowitz etal. 1999, p. 13486). In other words, this study putatively
showed that a natural metabolite could reverse some of the damage caused by a spi-
nal cord injury by supplanting axonal formations and reestablishing connections in a
spinal cord. However, Steward and colleagues, with the backing of FORE-SCI, did
not measure any effect of this sort, reporting: “inosine-treated rats did not exhibit
the transmidline sprouting reported in the original study” (2012b, p. 663). This was
despite their best efforts to match the components of the original study.
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D.Colaço et al.
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While they note that “there are no technical explanations for [their] failure to
detect the growth reported by Benowitz etal.,” Steward and colleagues still go
on to consider some of the “technical details” that the original and replication
studies might not share (2012b, p. 672). First, Steward and colleagues cite differ-
ences between the rats used in the original study and replication. Despite acquir-
ing the same strain from the same vendor, they propose that genetic drift may
have led to changes during the 12years between the respective studies. Second,
the replicators suggest that rat rearing and preparation were possibly different.
Third, the replicators could not rule out potential differences between the lesions,
despite their attempts to match the methods by which they induced these lesions.
Fourth, differences between how the axonal formations were traced and labeled
between the respective studies were cited, though Steward and colleagues suggest
that there is no obvious reason the mismatch of outcomes should depend on these
differences.
Benowitz, the principal researcher of the original study, responded to this
reported replication failure. He notes that “the study by Steward et al. is done
carefully but differs from the original study in two ways that may have contrib-
uted substantially to the divergent result” (Benowitz 2012, p. 674). These differ-
ences are mentioned above: rearing conditions and labeling technique. Benowitz
also suggests that how the midline was determined in the rats and the data analy-
sis might have contributed to the failure to replicate as well. While Benowitz sug-
gests these differences may explain the reported replication failure, he provides
no evidence in defense of this claim in his response.
This consideration of differences is representative of the reasons presented in
the concluding FORE-SCI report: overall, 11 reasons for failures to replicate are
stated (Steward etal. 2012a, p. 601). These include:
1. Type-1 errors
2. Differences in experimental details between original study and replication
3. Greater variability in the replication as compared to original study
4. Mistakes by replicators who were unskilled in using injury models or methods
5. Differences in animal models between original study and replication
6. Differences in lesions between original study and replication
7. Differences in care for animals between original study and replication
8. Differences in reagents between original study and replication
9. Bias
10. A non-robust effect
11. Scientific misconduct
Thus, while statistical (and ethical) reasons appear, this list highlights a much
greater focus on differences between the experimental components of original
studies and replication attempts.
While we focus on FORE-SCI in this paper, researchers’ tendency to cite study
differences in efforts to explain a failure to replicate can be found in other areas
of cognitive science and neuroscience as well. When skeptics (Karin-D’Arcy and
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Povinelli 2002) discuss difficulties in replicating animal mindreading studies
that deploy competitive feeding paradigms (Hare etal. 2001), Heyes claims that
“these difficulties suggest that the published reports… have not contained suffi-
cient detail to allow their methods to be reproduced in other laboratories” (2015,
p. 316; see also Halina 2021). In the history of neuroscience, failures to replicate
undermined claims that memories can be transferred. In response, proponents
claimed that all failures to replicate were due to differences between original and
follow-up studies (Colaço 2018, p. 36). In psychology, the field wherein the bulk
of recent replication debates have taken place, study population differences rou-
tinely are cited as explanations for reported replication failures, though they may
be met with skepticism (Owens 2018). Together, these cases support the claims
that the “reaction of some scientists whose work fails to replicate is to empha-
size that the replication attempts introduce substantive variations that explain the
failures” (Romero 2019, p. 5) and “if a direct replication fails to obtain the same
result as the original study, researchers may question… whether there is a misun-
derstanding about the understanding of the essential features required to produce
an effect” (Zwaan etal. 2018, p. 4). These examples supply evidence that the
FORE-SCI cases are not anomalies, and we invite readers to consider whether
scientists attempt to explain replication failures in terms of study differences in
their field.
Invoking differences in these kinds of cases also resembles, at least rhetorically,
responses to other alleged scientific failures that philosophers of science address.
For instance, many of the responses in FORE-SCI are akin to Duhem’s claims about
underdetermination. Just as a disconfirmation or failed prediction leaves open the
opportunity for researchers to blame an auxiliary assumption rather than their main
hypothesis (Ariew 1984), FORE-SCI’s troubling results leave open the opportu-
nity for researchers to blame the differences between original and follow-up studies
rather than anything to do with the reliability of the original study (or for that matter
the ethical character of its researchers).
Assessing apurported mismatch explanation
The FORE-SCI example and accompanying discussion in Sect.3 show that research-
ers often cite differences between experimental components in their attempts to
explain reported replication failures. This is problematic, as no replication can be
exact.4 It also meets neither of our conditions for a mismatch explanation. There is
no reason for us to think these differences are difference makers, nor is there consid-
eration of whether they are relevant. However, some FORE-SCI examples include
4 As Zwaan and colleagues note, “if a failed replication brings to light some factor that could potentially
affect the result and that differed between the original study and the replication… the post hoc considera-
tion of differences in features should lead to new testable hypotheses rather than blanket dismissals of the
replication result” (2018, p. 6).
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a search for difference makers. We analyze one of these cases, which resulted in a
“successful replication.”
When researchers search fordifferences
A group of FORE-SCI researchers set out to replicate a study designed to test the
role of sulfonylurea receptor 1-regulated (SUR1-regulated) cation channels in pro-
gressive hemorrhagic necrosis, or PHN (Simard etal. 2007). This form of necrosis,
resulting from acute spinal injury, leads to “devastating loss of spinal cord tissue,
cystic cavitation of the cord, and debilitating neurological dysfunction” (Simard
etal. 2007, p. 2105). The original study reports that the activity of SUR1-regulated
channels can be controlled via the inhibition of SUR1 by the drug glibenclamide
(Simard etal. 2007, p. 2109; Popovich etal. 2012, p. 615). When this inhibitor was
tested, necrosis and its consequences were reduced. As the original researchers put
it, the “block of SUR1 is associated with significant improvements in all of the char-
acteristic manifestations of PHN” (Simard etal. 2007, p. 2111). Based on these find-
ings, the original researchers claim that SUR1-regulated channels are a suitable tar-
get for spinal cord injury therapy and that glibenclamide is “especially attractive for
translational use in human SCI [spinal cord injury]” (Simard etal. 2007, p. 2112).
Popovich and colleagues set out to replicate Simard and colleagues’ study “in
which glibenclamide was found to limit PHN in a model of rat cervical contusion
injury” (Popovich et al. 2012, p. 615). They were able to do so in the end: like
Simard and colleagues, they determined that glibenclamide can limit PHN. How-
ever, Popovich and colleagues initially reported a failure to replicate, as there were
no “differences in the magnitude of intraspinal hemorrhage between” experimen-
tal and control groups (2012, p. 619). Only after “extensive discussions” with the
principal researchers of the original study did the two teams discover a potential
mismatch: Popovich and colleagues induced contusion injuries in a manner that was
dissimilar to the original study. The original study induced the injury at about a 5°
angle deviation from the dorsoventral axis of the spinal cord (see Fig.1), while the
initial replication attempt induced the injury parallel to the dorsoventral axis (Popo-
vich etal. 2012, p. 619). Though several factors suggest they cause the same injury,
these two methods differently induce contralateral damage to the spinal cord. Fur-
ther, the original method proved difficult to execute because it departs from more
standardized means of inducing spinal cord injury. Following this discovery, the
Fig. 1 Visualization of injury
induction in Simard etal. (2007)
versus Popovich etal. (2012)
(image generated via biorender.
com)
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research teams from the original study and replication worked together to match the
method in subsequent replication attempts.
Simard and Gerzanich, who performed the original study and informed the later
replication attempts, responded to Popovich and colleagues’ report. They note that
their description of methods in their original study (Simard etal. 2007) insufficiently
detailed the injury induction, which explains why Popovich and colleagues did not
match this method until after their discussion (Simard and Gerzanich 2012). How-
ever, this was not viewed as an omission in the original report. In their response,
Simard and Gerzanich note: “we simply assumed that any unilateral injury would
produce this result. We didn’t realize that some unilateral injuries could lead to
immediate bilateral hemorrhage that would mask contralateral spread of hemor-
rhage” (2012, p. 623). They go on to ask whether “the requirement for an identical
injury in the replication experiment [implies] that other injuries would not be ben-
efited by treatment with glibenclamide,” to which they answer that “it depends on
the question being asked, and the outcome being measured” (Simard and Gerzanich
2012, p. 623). With this irresolute answer, they list several caveats to the scope of
their original outcome.
Analyzing this case
Certainly, there is a difference between the injury method in the original study and
the initial attempt to replicate it. However, does it meet both conditions for a mis-
match explanation? In this case, researchers tested whether the change in injury
method varied with the change in outcome. When the same injury method was used,
the outcome was matched in a later follow-up. In this follow-up, the replicators
revised how their replication attempts were performed, which required a significant
degree of experimental expertise that came from the original researchers. Determin-
ing the difference in injury method was neither a speculation nor an ad-hoc excuse,
and it turned out to be a difference maker. Thus, the difference maker condition is
satisfied.
What about the relevance condition? The report of the original study lacks detail
on this study’s scope and the representativeness of its components. Given the trans-
lational aspirations of the original study, we can speculate that the intervention and
treatment should represent human clinical cases where spinal cord injuries occur
at a variety of angles (Smith etal., 2005). This vagueness is evidence for the con-
cern that scientists often do not clarify whether experimental components are fixed
or random factors (Machery 2020, p. 561). However, speculation is not necessary,
as Simard and Gerzanich admit that they assumed that any unilateral injury would
result in the same outcome. Likewise, in the report of the original study, they make
broad statements about the scope of their findings, stating that the “block of SUR1
is associated with significant improvements in all of the characteristic manifesta-
tions of PHN” (Simard etal. 2007, p. 2111, emphasis added). They do not specify
that their results might only apply to subtypes of spinal cord injuries, such as unilat-
eral, cervical, or of only a specific impact angle. Given these concluding statements,
one could argue that any method of spinal cord injury that induces PHN should be
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considered part of the population that is representative based on the stated, intended
scope. A spinal cord injury that deviated only by 5° but maintained similar level
(cervical) and impact energy is well within the bounds of being representative. Fur-
thermore, Popovich and colleagues used a unilateral injury method, which is repre-
sentative of the population of injury methods akin to the original study. Thus, this
case does not satisfy the relevance condition. Consistent with Machery’s resampling
account, the injury method is not a fixed factor. Simard and colleagues were not
studying whether PHN caused by the specific injury they induced can be treated
with glibenclamide. Rather, and based on their own comments, the injury method is
a random factor, one chosen by the original researchers from a population of meth-
ods as representative of any unilateral injury. On our account, the original follow-up
is a failure to replicate, and a mismatch explanation is not appropriate in this case.
It was only after the original researchers and replicators determined that the
injury method is a difference maker that they suggested it should be treated as a
fixed rather than random factor. This fact highlights that their discovery of a dif-
ference maker led both research groups to explain the initial failure in terms of the
match of the injury method. When this injury method was later matched, they called
the case a successful replication. At the same time, the relevance condition has not
been prioritized. Even though the responses from the original researchers and the
replicators suggest that they both assumed that the findings would generalize to
a variety of spinal cord injuries, this fact is not considered at all when they claim
to successfully replicate the original study in the end. Thus, this case provides an
example of how difference makers can be prioritized over the relevance of a poten-
tial mismatch.
Why some study dierences don’t matter forreplication
In Sect.2, we presented two conditions for when a mismatch serves as an appropri-
ate probe into whether a follow-up study counts as a bona fide replication attempt:
the difference maker condition and the relevance condition. The case in Sect.4 sat-
isfies only the difference maker condition. For this reason, we argue that it is not a
defensible mismatch explanation. It is an example of why discovering a difference
maker alone does not entail that a mismatch explanation is appropriate.
The importance oftherelevance condition
At this point, the reader might object to the relevance condition. After all, the
researchers in this case identified a component difference between the original study
and the follow-up that is demonstrably a difference maker for their respective out-
comes. Beyond quibbles about what really counts as a ‘mismatch,’ this case resulted
in an explanation of the mismatch of outcomes that is not due to the unreliability
of the original study. Even if there was some vagueness initially about the repre-
sentativeness of the original injury method, why should this case not be explained in
terms of the identified mismatch?
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This objection is consistent with FORE-SCI researcher responses. In Sect. 4,
a concern about the exact way the spinal cord injury is induced in rats was the
response of the original researchers. This focus on differences also is illustrated
by Benowitz’s reaction to the failure to replicate, discussed in Sect.3. It further is
reflected in the 11 reasons supplied above; six of them directly cite study differ-
ences. One may try to explain this ratio by arguing that within a single experimen-
tal approach, differences may be myriad, but there is only one way that replicators
could attribute replication failure to a false positive, or similarly perhaps only one
way to accuse someone of fraud. However, the list includes general differences, such
as the difference between experimental details expressed in (2), while at the same
time, the list cites specifics in (5), (6), (7), and (8). Even though (2) encompasses (5)
through (8), the authors nonetheless included these as separate reasons. Similarly,
the replicators could have devised several specific ways in which the methods or
results could be manipulated, but they offered only (11) to encompass all the actions
that could be categorized as misconduct.
While this objection may seem appealing, it reveals serious concerns with an
endeavor to explain all reported replication failures solely in terms of difference
makers. In this case, the original study can be counted as having a successful rep-
lication if one more narrowly construes the scope of the original’s outcomes after
the fact. This amounts to a post-hoc reappraisal of Simard and colleagues’ conclu-
sions only applying to a subtype of spinal cord injury rather than all injuries. This
comparatively narrow outcome is not consistent with what the original researchers,
by their own admission, assumed. Only after the initial failure to replicate and the
discovery of a difference maker did the original researchers recognize that the injury
method is not representative of all unilateral injuries.
At first glance, this situation might seem unproblematic. In fact, the reader might
be sympathetic to researchers’ interests in uncovering difference makers and better
controlling for them, further supporting this objection. These are admirable prac-
tices, but we argue that their application to replication comes at a cost. This cost is
material: researchers must spend time, money, and resources hunting down potential
difference makers. In the FORE-SCI studies, including the two we have detailed,
many differences were pursued (Steward etal. 2012a, p. 600), but only one differ-
ence maker was discovered amongst 12 replication attempts. Thus, despite the time,
money, and resources spent, the researchers’ endeavors to hunt down difference
makers largely did not help them in explaining the preponderance of failures to rep-
licate in FORE-SCI.
More importantly, this cost is also epistemic. If researchers care only about dif-
ference makers, they open the opportunity to undermine other epistemic aims, such
as translation. This is ironic, as the motivating concern for FORE-SCI was to deter-
mine why “not one of the many strategies reported as having promising effects were
translated into successful therapies” in humans (Steward etal. 2012a, p. 597).
Why might translation suffer when researchers focus exclusively on difference
makers, regardless of whether they satisfy the relevance condition? Translatabil-
ity is the epistemic aim of extending study outcomes to clinical contexts. For
FORE-SCI, the aim is to extend outcomes on treatment of spinal cord injuries
in rodent model organisms to human patients who have these injuries. For this
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D.Colaço et al.
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translation to be successful, the outcomes of the study must have a scope that
extends to these clinical contexts. Correspondingly, the components of the study
must be representative of the kinds of clinical conditions through which human
spinal cords are damaged. The treatment must be effective on spinal cord injuries,
rather than merely on one kind of spinal cord injury in rats. If one disregards the
relevance condition and merely narrows representativeness and scope in the face
of a difference maker, one thus ignores what clinical contexts one’s research can
translate to and possibly might undercut any translational aim one has.
These consequences of disregarding the relevance condition can be shown
with the FORE-SCI case. Initially, researchers claimed that an intervention
reduced, remediated, or resolved spinal cord injury. However, researchers cannot
make claims of such generality after focusing on difference makers and disre-
garding the relevance condition. Many components that were initially taken to be
broadly representative random factors now must be reconstrued. Thus, research-
ers can no longer claim that “the drug improves a spinal cord injury symptom.”
Instead, they can only say that “the drug improves a symptom of a very particular
kind of spinal cord injury in organisms that are of a specific species and strain,
have been manipulated in a very particular way, and reared in a specific colony,
etc.” While the first claim shows promise for translating to the clinic, the latter
raises many questions. Do humans exhibit these symptoms in the same manner
and chronology? Do humans receive spinal cord injuries like the kind induced
in the original study? Are any of the specified rodent rearing conditions akin to
human development?
This is not to say that the answers to these questions are necessarily “no,” or
that the research entirely lacks translational value. Translation is distinct from the
epistemic aim of inductive generalization, as translation can be achieved even if the
study’s outcomes do not apply to diverse kinds of clinical contexts. For instance,
humans suffer common but characteristic brain injuries, such as when an unbuck-
led driver predictably sustains a frontal injury after hitting the steering wheel with
their forehead during a car accident. Studies using an injury induction method that is
representative of this specific, real-world scenario might translate into therapies for
humans with this very specific, but also quite common, injury, even if they do not
generalize to all, or any other, types of brain injuries. This feature of translation is
akin to the epistemic aim of extrapolation, which is best motivated by anatomical or
mechanistic similarities between the model and target systems (Steel 2007).
Nonetheless, for the case from FORE-SCI that we recounted in Sect.4, trans-
lation will be much more limited than the authors of the original report stated or
implied. Given that translation concerns motivated FORE-SCI, and there is no rea-
son to think that a 5° angle deviation from midline in cervical injury in rats repre-
sents some clinically important factor of human spinal cord injuries independently
of it being a difference maker, researchers likely will not promote translation if
they disregard the relevance condition (short of a major and surprising discovery).
More seriously, disregarding the relevance condition might result in researchers not
addressing the clinical extension of their study outcomes. They may focus only on
the difference makers themselves, rather than what these difference makers represent
in the clinical contexts to which they want their research to translate.
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When should researchers cite study differences inresponse… Page 13 of 17 39
Do we think researchers should never investigate difference makers? No; learn-
ing about difference makers is undoubtedly important in the generation of scientific
knowledge. However, we are skeptical of explaining all reported replication failures
in terms of difference makers without considering the relevance condition. If one
merely takes any difference maker to explain differences between studies’ outcomes,
we are no longer talking about the replication of studies that have scopes beyond the
literal components of the studies and their interactions. There is no assessment of
the reliability of a study with a certain scope if that scope is so malleable post hoc,
and we argue that this is a significant loss to how we should understand not only
reliability but also other epistemic aims like translation, generalization, and robust-
ness. Even if researchers gain scientific knowledge about these difference makers,
they give up on the extension of these difference makers to diverse experimental
contexts, let alone clinical ones. Thus, we do not deny that difference makers matter,
but we think that they do not always matter for replication.
Our distinction between the general scientific value of difference makers and
their importance in diagnosing replication attempts answers a question the reader
might have about the strength of our thesis. That seemingly similar injury induction
methods result in different outcomes might interest researchers. For this reason, they
may ask whether this difference maker reflects something important for the study
of spinal cord injuries.5 If the difference maker indeed reflects something impor-
tant, it could be consequential for their epistemic aims, including translation. We
do not deny this possibility. If researchers wish to investigate how two (or more)
injury induction methods can result in different outcomes, they should do so. They
might discover something interesting about these methods in the process. What they
should not do, however, is take this difference maker alone to resolve a reported rep-
lication failure.
There are other reasons to be skeptical of explaining all replication failures in
terms of difference makers. A focus on differences limits discussion of statistical
standards, of combating questionable research practices, revising how methods are
reported, or more precisely reporting the scope of conclusions. Likewise, focus-
ing on differences assumes that the original study was correct, which illustrates “a
tacit assumption…that the original study is a flawless, expertly performed piece of
research that reported a true effect” (Zwaan etal. 2018, p. 6). Indeed, as we saw
here, this focus is perhaps exacerbated when testing differences leads to the discov-
ery of a difference maker. In such cases, the original studies persist in some form,
albeit with an outcome of much narrower scope, leading to a pseudo-resolution that
allows researchers to downplay any issues beyond the difference. It is here we see
that invoking mismatch explanations is akin to Duhem’s claims about blaming aux-
iliary assumptions in efforts to “save” research.
There are also practical reasons to be skeptical of explaining all failures to rep-
licate in terms of difference makers. There are potentially unlimited differences
between two studies’ components, which might not explain a mismatch in their out-
comes, and there is only so much time and so many resources researchers can devote
5 We thank an anonymous reviewer for raising this question.
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D.Colaço et al.
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to pursuing these differences while neglecting other epistemic aims. Researchers
may be better off accepting that a failure of a reasonable effort to replicate shows
that an original study is unreliable given its scope, after which they can change their
methods or address other claims that might fulfill their full set of epistemic aims.
Our claims are consonant with those of philosophers and scientists who argue
that pursuing replication should not lead us to overlook other epistemic aims, such
as validity (Feest 2019) or generalizability (Yarkoni 2019). However, we do not
challenge the importance of replication. By contrast, we recognize its importance
and the corresponding importance of how researchers respond to reported replica-
tion failures. Reliability is just one of several epistemic aims, but it is important.
Mismatch explanations can be defensible. However, citing differences without con-
sideration of relevance can undercut other epistemic aims. This is the case even if
looking for difference makers seems, at first glance, appropriate. The concern that
researchers will focus on difference makers at the expense of representativeness and
scope of studies is pronounced in neuroscience, where translation is often a long-
term epistemic aim, organisms are frequently deployed, and a multiplicity of experi-
mental protocols (Sullivan 2009) make salient the myriad ways in which two studies
can differ.
Our recommendation
For a positive conclusion, we propose a method for how researchers should approach
replication and figure out whether a mismatch explanation is appropriate. Before a
replication is attempted, replicators should present an experimental protocol to the
original researchers and ask these researchers if the protocol matches the original
study. Original researchers can check whether fixed factors are matched and whether
random factors are representative of the population of the original study’s ran-
dom factors. A discussion should then be given to factors identified by the original
researchers as having to be altered to match appropriately, and particular attention
should be given to the extent to which these factors are allowed to vary and how
such freedom or constraint might affect the scope and other epistemic aims of the
research.
Our proposal capitalizes on the fact that the difference maker and relevance
conditions are independent of one another. Because a difference can be a differ-
ence maker without satisfying the relevance condition and vice versa, researchers
can resolve whether the relevance condition is met before any difference makers are
found. Doing this first prevents the possibility that researchers will explain a pos-
sible failure to replicate in terms of a difference maker simply because this differ-
ence maker has been discovered or even merely speculated upon. It also prevents
researchers needlessly spending time, money, and resources hunting down potential
difference makers that are irrelevant to explaining reported replication failures.
Our proposal resolves the potential issue that researchers can be vague about the
exact scope of the original study’s outcomes and its components’ representative-
ness. Researchers might find it difficult to express these commitments a priori and
in the abstract, but this proposal requires them only to identify whether a particular
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When should researchers cite study differences inresponse… Page 15 of 17 39
component is representative of the appropriate population. By comparing a particu-
lar experimental protocol to another protocol, the exact scope and representativeness
of the original study need not be precisely stated.
Our proposed method would not stop mismatches from occurring. Research-
ers still might inadvertently introduce non-matching components into their stud-
ies. However, our proposal supplies an answer to how difference makers should be
evaluated if, or perhaps even before, they are discovered. If these differences do not
fulfill the relevance condition and this fact is discussed ahead of time, they cannot be
invoked as part of a mismatch explanation. And, if difference makers are discovered,
researchers still can investigate them. Nothing about our recommendation, and noth-
ing about our concerns with inappropriate appeals to mismatch explanations more
generally, suggests that researchers should not pursue difference makers as a means
of generating scientific knowledge. However, they should investigate them because
they are independently interesting, not because they explain a reported replication
failure.
Conclusion
Though mismatch explanations might seem like the scapegoating of the inevitable
differences between studies, there are cases where these explanations are appropri-
ate. However, they are not always appropriate, and citing differences can undermine
other epistemic aims. Given the generality with which scientists often present their
outcomes, we should take seriously these potential negative consequences when cit-
ing study differences. If an epistemic aim like translation is the end goal, as it was in
FORE-SCI, then citing irrelevant differences, even when they are difference makers,
may move scientists farther from this goal.
While we stress the potential negative consequences of citing study differences,
we do not fault the individual scientists who do this. We speculate that scientific dis-
ciplines favor a focus on differences for at least three reasons. First, as noted above,
sometimes seeking out and correcting component differences is defensible. There
are special cases when these may be the most salient aspect to pursue, such as when
an experimental method involves a new technique or technology, making it more
likely that the methods are not fully disseminated in detail or that replicating labs
may take some time to perfect their use of a new technique. Likewise, difference
makers can be worth pursuing for scientific aims that are independent of reliability
or replication. For this reason, it is perhaps not surprising that researchers might
erroneously equate an interesting difference maker with one relevant to diagnosing a
replication attempt.
Second, the endeavor to replicate another’s work may be viewed by researchers in
terms of a “prove or disprove” mentality. Despite attempts to portray replication in
a neutral, blameless manner, the goal after a failure to replicate may be less “is this
outcome reliable?” and more “how did the original team mess up (or lie)?” Citing
differences supplies a means of placing the error in the precision of the replication,
rather than blaming the original researchers for incompetent or immoral research
practices. Indeed, the penalties for dishonesty are harsh (and one could certainly
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D.Colaço et al.
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39 Page 16 of 17
argue that they should be), but even a whiff of dishonesty can ruin careers. Thus,
there may be reluctance among anyone suspicious of an original study to become an
accuser of scientific incompetence or fraud.
Third, placement of the error on differences also alleviates the entire field of
researchers from blame for systemic practices, such as publication bias or undue
focus on novelty in grant funding, which may contribute to failures of replication or
even a lack of attempts at replication. This might explain why programs like FORE-
SCI are uncommon, as funding often is not provided for research focused solely on
replication, and why failures to replicate often go unpublished. If these speculations
are correct, they suggest that there may be a need for us to consider the importance
or value of replication as it relates to replication failures.
Acknowledgements Thanks to Carl Craver, Christopher Dorst, and two anonymous referees for their
comments on an earlier draft of this paper. This paper was presented at the 2021 meeting of the Interna-
tional Society for the History, Philosophy, and Social Sciences of Biology. Thanks to those who provided
feedback at this event. Corresponding author David Colaço is funded by the Alexander von Humboldt
Foundation. Co-author Bradley Walters is funded by the Joe W. and Dorothy Dorsett Brown Foundation.
Funding Open Access funding enabled and organized by Projekt DEAL. Corresponding author David
Colaço is funded by the Alexander von Humboldt Foundation. Co-author Bradley Walters is funded by
the Joe W. and Dorothy Dorsett Brown Foundation.
Open Access This article is licensed under a Creative Commons Attribution 4.0 International License,
which permits use, sharing, adaptation, distribution and reproduction in any medium or format, as long as
you give appropriate credit to the original author(s) and the source, provide a link to the Creative Com-
mons licence, and indicate if changes were made. The images or other third party material in this article
are included in the article’s Creative Commons licence, unless indicated otherwise in a credit line to the
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not permitted by statutory regulation or exceeds the permitted use, you will need to obtain permission
directly from the copyright holder. To view a copy of this licence, visit http:// creat iveco mmons. org/ licen
ses/ by/4. 0/.
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