The “replication crisis” in various areas of research has been widely discussed in journals over the past decade [see, for example, Gilbert et al., 2016; Baker, 2016; Open Science Collaboration, 2015; Munafò et al., 2017]. At the center of this crisis is the concern that any given scientific result may not be reliable; in this way, the crisis is ultimately a question about the collective confidence we have in our methods and results (Alipourfard et al., 2012). The past decade has also witnessed many advances in data science, and “big data” has both contributed to concerns about scientific reliability (Bollier and Firestone, 2010; Calude and Longo, 2017) and also offered the possibility of improving reliability in some fields (Rodgers and Shrout, 2018).

In this article we discuss scientific progress in the clinical neurosciences, and focus on an example related to traumatic brain injury (TBI). Using this example, we argue that the rapid pace of work in this field, coupled with a failure to directly test and eliminate (falsify) hypotheses, has resulted in an expansive literature that lacks the precision necessary to advance science. Instead, we suggest that falsification – where one develops a strong hypothesis, along with methods that can test and refute this hypothesis – should be used more widely by researchers. The strength of a hypothesis refers to how specific and how refutable it is (Popper, 1963; see Table 1 for examples). We also argue for greater emphasis on testing and refuting strong hypotheses through a “team science” framework that allows us to address the heterogeneity in samples and/or methods that makes so many published findings tentative (Cwiek et al., 2021; Bryan et al., 2021).

Hyperconnectivity hypothesis in brain connectomics

To provide a specific example for the concerns outlined in this critique, we draw from the literature using resting-state fMRI methods and network analysis (typically graph theory, see Caeyenberghs et al., 2017 to examine systems-level plasticity in TBI). Beginning with one of the first papers combining functional neuroimaging and graph theory to examine network topology (Nakamura et al., 2009), an early observation in the study of TBI was that physical disruption of pathways due to focal and diffuse injury results in regional expansion (increase) in strength or number of functional connections. This initial finding was observed in a small longitudinal sample, but then similar effects were observed in other samples (Mayer et al., 2011; Bharath et al., 2015; Hillary et al., 2015; Johnson et al., 2012; Sharp et al., 2011; Iraji et al., 2016) and animal models of TBI (Harris et al., 2016). These findings were summarized in a paper by one of the current authors (FGH) outlining potential mechanisms for hyperconnectivity and its possible long-term consequences, including elevated metabolic demand, abnormal protein aggregation and, ultimately, increased risk for neurodegeneration (see Hillary and Grafman, 2017). The “hyperconnectivity response” to neurological insult was proposed as a possible biomarker for injury/recovery in a review summarizing findings in TBI brain connectomics (Caeyenberghs et al., 2017).

Nearly simultaneously, other researchers offered a distinct – in fact, nearly the opposite – set of findings. Several studies of moderate to severe brain injury (as examined above) found that white matter disruption during injury resulted in structural and functional disconnection of networks. The authors in these papers outline a “disconnection” hypothesis: the physical degradation of white matter secondary to traumatic axonal injury results in reduced connectivity of brain networks, which is visible both structurally in diffusion imaging studies (Fagerholm et al., 2015) and functionally using resting-state fMRI approaches (Bonnelle et al., 2011). These findings were summarized in a high-profile review (Sharp et al., 2014) where the authors argue that TBI “substantially disrupts [connectivity], and that this disruption predicts cognitive impairment …”.

When juxtaposed, these two hypotheses hold distinct explanations for the same phenomenon with the first proposing that axonal injury results in a paradoxically enhanced functional network response and the second that the same pathophysiology results in reduced functional connectivity. Both cannot be true as they have been proposed, so which is correct? Even with two apparently contradictory hypotheses in place, there has been no direct testing of these positions against one another to determine the scenarios where either may have merit. Instead, each of these hypotheses remained unconditionally intact and served to support distinct sets of outcomes.

The most important point to be made from this example is not that competing theories in this literature exist. To the contrary, having competing theories for understanding a phenomenon places science in a strong position; the theories can be tested against one another to qualify (or even eliminate) one position. The point is that there have been no attempts to falsify either a hyperconnectivity or disconnection hypothesis, allowing researchers to evoke one or the other depending upon the finding for a given dataset (i.e., disconnection due to white matter loss, or functional “compensation” in the case of hyperconnectivity). What has contributed to this problem is that increasingly complex computational modeling also increases the investigator degrees of freedom, both implicitly and explicitly, to support their hypotheses. In the case of the current example of neural networks, these include selection from a number of brain atlases or other methods for brain parcellation and likewise numerous approaches to neural network definition (see Hallquist and Hillary, 2019). Figure 1 provides a schematic representation of two distinct and simultaneously supported hypotheses in head injury.

Figure 1

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To be clear, the approach taken by investigators in this TBI literature is consistent with a research agenda designed to meet the demands for high publication throughput (more on this below). Examiners publish preliminary findings but remain appropriately tentative in their conclusions given that the sample is small and unexplained factors are numerous. Indeed, a common refrain in many publications is the “need for replication in a larger sample”. As opposed to pre-registering and testing strong hypotheses, investigators are reinforced to identify significant results (any result) for publication. In brain injury work examining network plasticity, investigators have often made general claims that brain injury results in “different” or “altered” connectivity (a problem dating back to early fMRI studies in TBI; Hillary, 2008). While unintentional, imprecise hypotheses increase the likelihood that chance findings are published. The primary consequence is that all findings are “winners”, permitting growing support for either position without movement toward resolution.

Overall, the TBI connectomics literature presents a clear example of a failure to falsify and we argue that it is attributable, at least in part, to the publication of large numbers of papers reporting the results of studies in which small samples were used to examine under-specified hypotheses. This “science-by-volume” approach is exacerbated by the overuse of inappropriate statistical tests, which increases the probability that spurious findings will be reported as meaningful (Button et al., 2013).

The challenges outlined here, where there is a general failure to test and refute strong hypotheses, are not isolated to the TBI literature. Similar issues have been expressed in preclinical studies of stroke (Corbett et al., 2017) in the translational neurosciences where investigators maintain flexible theory and predictions to fit methodological limitations (Macleod et al., 2014; Pound and Ritskes-Hoitinga, 2018; Henderson et al., 2013), and in cancer research where only portions of published data sets provide support for hypotheses (Begley and Ellis, 2012). These factors have likely contributed to the repeated failure of clinical trials to move from animal models to successful Phase III interventions in clinical neuroscience (Tolchin et al., 2020). This example in the neurosciences also mirrors the longstanding problems of co-existing yet inconsistent theories in other disciplines like social psychology (see Watts, 2017).

Operating without anchors in a sea of high-volume science

One challenge then is to determine where the bedrock of our field (our foundational knowledge) ends, and where areas of discovery that show promise (but have yet to be established) begin. By some measure neurology is a fledgling field in the biological sciences: the publication of De humani corporis fabrica by Vesalius in 1543 is often taken to mark the start of the study of human anatomy (Vesalius, 1555) Jean-Martin Charcot – often referred to as the “founder of neurology” – arrived approximately 300 years later (Zalc, 2018). If we simplify our task and start with the work of Milner, Geschwind and Luria in the 1950s, it is still a challenge to determine what is definitively known and what remains conjectural in the field. This challenge is amplified by the pressure on researchers to publish or perish (Macleod et al., 2014; Kiai, 2019; Lindner et al., 2018). The number of papers published per year continues to increase without asymptote (Bornmann and Mutz, 2015). When considering all papers published in the clinical neurosciences since 1900, more than 50% of the entire literature has been published in the last 10 years and 35% in the last five years (see supplementary figures S1a,b in Priestley et al., 2022). In the most extreme examples, “hyperprolific” lab directors publish a scientific paper roughly every 5 days (Ioannidis et al., 2018). It is legitimate to ask if the current proliferation of published findings has been matched by advances in scientific knowledge, or if the rate of publishing is outpacing scientific ingenuity (Sandström and van den Besselaar, 2016) and impeding the emergence of new theories (Chu and Evans, 2021).

We argue that a culture of science-by-volume is problematic for the reliability of science, primarily when paired with research agendas not designed to test/refute hypotheses. First, without pruning possible explanations through falsification, the science-by-volume approach creates an ever-expanding search space where finite human and financial resources are deployed to maximize breadth in published findings as opposed to depth of understanding (Figure 2A). Second, and as an extension of the last point, failure to falsify in a high-volume environment challenges our capacity to know which hypotheses represent foundational theory, which hypotheses are encouraging but require further confirmation, and which hypotheses should be rejected. Finally, in the case of the least-publishable-unit (Broad, 1981) a single data set may be carved into several smaller papers resulting in circles of self-citation and the illusion of reliable support for a hypothesis (or hypotheses) (Gleeson and Biddle, 2000).

Figure 2

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There have even been efforts internationally to make science more deliberate through de-emphasis of publication rates in academic circles (Dijstelbloem et al., 2013). Executing this type of systemic change in publication rate poses significant challenges and may ultimately be counterproductive because it fails to acknowledge the advancements in data aggregation and analysis afforded by high performance computing and rapid scientific communication through technology. So, while an argument can be made that our rate of publishing is not commensurate with our scientific progress, a path backward to a lower annual publication rate seems an unlikely solution and ignores the advantages of modernity. Instead, we should work toward establishing scientific foundation by testing and refuting strong hypotheses and these efforts may hold the greatest benefit when used to prune theories to determine the fittest prior to replication (Figure 2B). This effort maximizes resources and makes the goals for replication, as a confrontation of theoretical expectations, very clear (Nosek and Errington, 2020a). The remainder of the paper outlines how this can be achieved with focus on several contributors to the replication crisis.

Metascience (Peterson and Panofsky, 2014) has become central to many of the issues raised here. Metascience uses the tools of science to describe and evaluate science on a macro scale and to motivate reforms in scientific practice (Munafò et al., 2017; Ioannidis et al., 2015; Gurevitch et al., 2018). The emergence of metascience is at least partially attributable to advances in web search and indexing, network science, natural language processing, and computational modeling. Amongst other aims, work under this umbrella has sought to diagnose biases in research practice (Larivière et al., 2013; Clauset et al., 2015; Huang et al., 2020), understand how researchers select new work to pursue (Rzhetsky et al., 2015; Jia et al., 2020), identify factors contributing to academic productivity (Liu et al., 2018; Li et al., 2018; Pluchino et al., 2019; Janosov et al., 2020), and forecast the emergence of new areas of research (Prabhakaran et al., 1959; Asooja et al., 2016; Salatino et al., 2018; Chen et al., 2017; Krenn and Zeilinger, 2020; Behrouzi et al., 2020).

A newer thread of ongoing efforts within the metascience community is working to build and promote infrastructure for reproducible and transparent scholarly communication (see Konkol et al., 2020 for a recent review, Wilkinson et al., 2016; Nosek et al., 2015). As part of this vision, primary deliverables of research processes include machine-readable outputs that can be queried by researchers for meta-analyses and theory development (Priem, 2013; Lakens and DeBruine, 2021; Brinckman et al., 2019). These efforts are coupled with recent major investments in approaches to further automate research synthesis and hypothesis generation. The Big Mechanism program, for example, was set up by the Defense Advanced Research Projects Agency (DARPA) to fund the development of technologies to read the cancer biology literature, extract fragments of causal mechanisms from publications, assemble these mechanisms into executable models, and use these models to explain and predict new findings, and even test these predictions (Cohen, 2015).

Lines of research have also emerged using creative assembly of experts (e.g., prediction markets; Dreber et al., 2015; Camerer et al., 2016; Camerer et al., 2018; Gordon et al., 2020 and AI-driven approaches Altmejd et al., 2019; Pawel and Held, 2020; Yang et al., 2020) to estimate confidence in specific research hypotheses and findings. These too have been facilitated by advances in information extraction, natural language processing, machine learning, and larger training datasets. The DARPA-funded Systematizing Confidence in Open Research and Evidence (SCORE) program, for example, is nearing the end of coordinated three-year long effort to develop technologies to predict and explain replicability, generalizability and robustness of published claims in the social and behavioral sciences literatures (Alipourfard et al., 2012). As it continues to advance, the metascience community may serve to revolutionize the research process resulting in a literature that is readily interrogated and upon which strong hypotheses can be built.

We have proposed that falsification of strong hypothesis provides a mechanism to increase study reliability. High volume science should ideally function to eliminate possible explanations, otherwise productivity obfuscates progress. But can falsification ultimately achieve this goal? A strict Popperian approach, that every observation represents either a confirmation or refutation of a hypothesis, is challenging to implement in day-to-day scientific practice (Lakatos, 1970; Kuhn, 1970). What’s more, one cannot, with complete certainty, disprove a hypothesis any more than one can hope to prove a hypothesis (see Lakatos, 1970). It was Popper who emphasized that truth is ephemeral and even when it can be accessed, it remains provisional (Popper, 1959).

The philosophical dilemma in establishing the “true” nature of a scientific finding is reflected in the pragmatic challenges facing replication science. Even after an effort to replicate a finding, when investigators are presented with the results and asked if the replication was a success, the outcome is often disagreement resulting in “intellectual gridlock” (Nosek and Errington, 2020b). So, if the goal to falsify a hypothesis is both practically and philosophically flawed, why the emphasis? The answer is that, while falsification cannot remove the foibles of human nature, systematic methodological error, and noise from the scientific process, by setting our sights on testing and refuting strong a priori hypotheses we may uncover the shortcomings to our explanations. Attempts to falsify through refutation cannot be definitive but the outcome of multiple efforts can critically inform the direction of a science (Earp and Trafimow, 2015) when formally integrated into the scientific process (as depicted in Figure 2).

Finally, falsification alone serves as an incomplete response to problems of scientific reliability but becomes a powerful tool when combined with efforts that maximize transparency in method, make null results available, facilitate data/code sharing, and increase the incentive structures for investigators to refocus on open and transparent science.

Due to several factors including a high-volume science culture and previously unavailable computational resources, the empirical sciences have never been more productive. This unparalleled productivity invites questions about the rigor and direction of science and, ultimately, how these efforts translate to scientific advancement. We have proposed that it should be a primary goal to identify the “ground truths” that can serve as a foundation for more deliberate study and, to do so, there must be greater emphasis on testing and refuting strong hypotheses. The falsification of strong hypotheses enhances the power of replication first by pruning options and identifying the most promising hypotheses including possible mechanisms. When conducted through a team science framework, the endeavor leverages shared datasets that allow us to address heterogeneity that makes so many findings tentative. We must take steps toward more transparent and open science including – and most importantly – study pre-registration of strong hypotheses. The ultimate goal is to harness the rapid advancements in big data, computational power, and strong, well-defined theory with the goal to accelerate science.

There are no data associated with this article.

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Thank you for submitting your article "How Failure to Falsify in High Volume Science contributes to the Replication Crisis" to eLife for consideration as a Feature Article. Your article has been reviewed by four peer reviewers, and the evaluation has been overseen by a member of the eLife Features Team (Peter Rodgers). The following individuals involved in review of your submission have agreed to reveal their identity: Robert Thibault; Jean-Baptiste Poline; Nishant Sinha; and Yujiang Wang.

The reviewers and editors have discussed the reviews and we have drafted this decision letter to help you prepare a revised submission.

Summary:

This manuscript is of broad interest to the scientific community and particularly engaging for the readers in neuroscience. As the number of scientific articles exploring new hypotheses grows exponentially every year, there have not been many attempts to select the most competent hypotheses while falsifying the others. The authors juxtapose two prevalent hypotheses in network neuroscience literature on brain injury as an example. The manuscript offers suggestions on selecting the most compelling hypothesis and directions for designing studies to falsify them. However, there are a number of points that need to be addressed to make the article suitable for publication.

Essential revisions:

1. Lines 55-62: Please give examples of strong and weak hypotheses. Please also explain why "hypotheses that are supported by a range of findings should be considered weak". You might also want to consider linking strong/weak hypotheses to the idea of "research questions", which can be broad and vague, as compared to "hypotheses" which should be more precise.

2. Lines 120-122: Are there any systematic reviews on this topic that use one (or several) strong hypotheses and then check if the various studies support the stronger hypothesis? (e.g., does area X change within timeframe Y, in Z types of patients)? Also, I don't think the issue here is that they lack power to refute hypotheses, but instead that this lack of power is coupled with many statistical tests, leading to false positives that are used to support weak hypotheses (e.g. that brain activity "changes").

3. Lines 230-232: This paragraph could benefit from having a concrete example of a strong hypothesis and a matching weak hypothesis. This will likely help the reader grasp the issue more concretely.

4. Line 261: I am confused by the statement "sample heterogeneity requires large diverse samples". What part of heterogeneity are you trying to address? If testing a treatment that will be deployed to a diverse population of TBIs, I get that you would want a diverse sample, but a diverse sample will increase heterogeneity.

5. Lines 280-282: Or…it might be almost all noise? If we take Button's 2013 finding of 8% power in neuroimaging studies, then differences in findings are more likely due to noise than to demographics or other characteristics.

6. One issue to consider is that the hypotheses considered in the TBI example seem to be too vague or formulated in a too general manner.

7. The interaction between publication incentivization and weak hypotheses is alluded to but leaves the reader unclear on the topic; please say more about this.

8. As noted in the last part of the paper, one of the common tool to limit false discovery is pre-registration. It is unclear why this is not emphasized in the core of the text, rather than lately, as a tool to *review* hypotheses.

9. The social mechanisms to lead us to "team science" are unclear – if this article is meant to help the research community to move in this specific direction, a practical path should be proposed, as "modification of mindset" is certainly more a goal than a practical approach.

10. Specifically, framing all of scientific research in neuroscience in terms of hypotheses that can be confirmed or refuted is limiting; and as the authors acknowledged, the answer might be not a clear yes/no. Please consider discussing how it is sometimes more productive to revise aspects of a particular hypothesis. Nevertheless, I agree with the underlying sentiment that a key to replication is being able to receive recognition for the effort and rigour rather than the outcome.

11. As a computational researcher I would also like to see a stronger emphasis on both:

i) how data, code, and informatics are creating some of the replication crisis;

ii) how stronger informatics frameworks may be part of the solution.

Just an anecdote from personal experience and years of headache: Our lab has been trying to apply a specific networks neuroscience approach called "structural covariance networks". We initially applied it to test the local hyperconnection hypothesis in ASD. It took us years to realise and acknowledge that the computational method itself is very problematic in terms of being replicable even in data from the same scanner, site etc., and despite controlling for every biological variable imaginable. It took us another year, and a very talented student, to understand that it is the method itself that enhances the noise in the data in a very "unuseful" way thus drowning any biological effect. We finally could publish this insight here: https://pubmed.ncbi.nlm.nih.gov/32621973/ I use this example to highlight that our "problem" could not really be framed as a hypothesis refuting exercise, as the real insight for us, and I hope also for the community, was not whether the original hypothesis was right or wrong, but that our tool was flawed.

12. The caption for Figure 2 is confusing, and the content of (Priestley et al., under review) is not clear; please delete this figure and add one or two sentences to the text to say that the number of papers in [subject] has increased from about XX per year in 1970 to YYY per year in 2020.

Essential revisions:

1. Lines 55-62: Please give examples of strong and weak hypotheses. Please also explain why "hypotheses that are supported by a range of findings should be considered weak". You might also want to consider linking strong/weak hypotheses to the idea of "research questions", which can be broad and vague, as compared to "hypotheses" which should be more precise.

This is an important point and based upon this feedback we work to address this issue in text, we now have ~line 57 and we now include a Table with examples.

“In the work of falsification, the more specific and more refutable a hypothesis is, the stronger it is, and hypotheses that can be supported by different sets of findings should be considered weak (Popper, 1963; see Table 1 for example of hypotheses).”

2. Lines 120-122: Are there any systematic reviews on this topic that use one (or several) strong hypotheses and then check if the various studies support the stronger hypothesis? (e.g., does area X change within timeframe Y, in Z types of patients)?

The lack of direct examination of this problem in the hyperconnectivity literature was a primary impetus for the current review. There has been no systematic effort to hold these positions (hyperconnectivity v. disconnection) side-by-side to test them.

Also, I don't think the issue here is that they lack power to refute hypotheses, but instead that this lack of power is coupled with many statistical tests, leading to false positives that are used to support weak hypotheses (e.g. that brain activity "changes").

This is an outstanding point and we agree that the sheer volume of statistical tests in a number of studies increases the probability that findings by chance are published as significant and important. On line 121, we have modified this statement to reflect this point to read:

“Overall, the TBI connectomics literature presents a clear example of a failure to falsify and we argue that it is attributable at least in part by science-by-volume, where small samples are used to examine non-specific hypotheses. This scenario is further worsened using a number of statistical tests which increases the probability that spurious findings are cast as meaningful [40,95].”

3. Lines 230-232: This paragraph could benefit from having a concrete example of a strong hypothesis and a matching weak hypothesis. This will likely help the reader grasp the issue more concretely.

This is an important point and one we discussed as a group prior to the initial submission. We agree completely that concrete examples help to understand the problem and have added several to the text and to Table 1 (line 63).

4. Line 261: I am confused by the statement "sample heterogeneity requires large diverse samples". What part of heterogeneity are you trying to address? If testing a treatment that will be deployed to a diverse population of TBIs, I get that you would want a diverse sample, but a diverse sample will increase heterogeneity.

This is a good point and we have worked to clarify this statement. The point is that small samples do not allow investigation of the effects of sex, education, age, and other factors. Larger, more diverse samples permit direct modeling of these effects. This statement now reads (line 276):

“Addressing sample heterogeneity requires large diverse samples for direct modeling of influencing factors and one avenue to make this possible is data sharing.”

5. Lines 280-282: Or…it might be almost all noise? If we take Button's 2013 finding of 8% power in neuroimaging studies, then differences in findings are more likely due to noise than to demographics or other characteristics.

This is an interesting point, but there does appear to be a there, there. A number of higher powered studies do track changes in connectivity that appear to be directly related to pathophysiology and, importantly, correlate with behavior. However, one cannot deny that at least a subset of these studies presents results that capitalize upon spurious signal or noise.

6. One issue to consider is that the hypotheses considered in the TBI example seem to be too vague or formulated in a too general manner.

The point made here by the Referee is not entirely clear. If this is a statement about the need for stronger hypotheses, we agree that greater specificity is needed and we hope to add context for this point by adding example hypotheses in Table 1. Alternatively, if the Reviewer aims to indicate that this is a TBI-specific phenomenon, that is also possible, though it is unclear why this would occur only in TBI within the clinical neurosciences.

7. The interaction between publication incentivization and weak hypotheses is alluded to but leaves the reader unclear on the topic; please say more about this.

This relationship is made more explicit with the passage on line 115:

“As opposed to pre-registering and testing strong hypotheses, investigators are compelled to identify significant results (any result) for publication. In brain injury work examining network plasticity, investigators have often made general claims that brain injury results in “different” or “altered” connectivity (a problem dating back to early fMRI studies in TBI; [Hillary, 2008]). While it is unlikely the intention, under-specified hypotheses increase the likelihood that chance findings are published. The primary consequence is that all findings are “winners”, permitting growing support for either position without movement toward resolution.”

8. As noted in the last part of the paper, one of the common tool to limit false discovery is pre-registration. It is unclear why this is not emphasized in the core of the text, rather than lately, as a tool to *review* hypotheses.

This is an excellent point, and we now make clear the importance of study preregistration at the outset of the paper (line 55) so that when we return to it, there is context.

9. The social mechanisms to lead us to "team science" are unclear – if this article is meant to help the research community to move in this specific direction, a practical path should be proposed, as "modification of mindset" is certainly more a goal than a practical approach.

We appreciate this point and agree that this statement is confusing. We have removed this statement.

10. Specifically, framing all of scientific research in neuroscience in terms of hypotheses that can be confirmed or refuted is limiting; and as the authors acknowledged, the answer might be not a clear yes/no. Please consider discussing how it is sometimes more productive to revise aspects of a particular hypothesis. Nevertheless, I agree with the underlying sentiment that a key to replication is being able to receive recognition for the effort and rigour rather than the outcome.

This is an important point. Part of the scientific process clearly requires revisions of our theory. As this reviewer alludes to, however, when we revise our hypotheses to fit our outcomes, we risk advancing hypotheses supported by spurious data. We see preregistration as part of the solution and based upon comments elsewhere in this critique, we have refocused on how preregistration can help not only in the development of strong hypotheses, but also in their modification. We also now include Table 1 to provide modern context for what might be considered a “falsifiable” hypothesis. We also include a section titled “Practical Challenges to Falsification” to make clear that falsification of strong hypotheses is one tool of many to improve our science.

11. As a computational researcher I would also like to see a stronger emphasis on both:

i) how data, code, and informatics are creating some of the replication crisis;

ii) how stronger informatics frameworks may be part of the solution.

We agree and now add a section to outline the parameters of this natural tension (see “Big Data as Friend and Foe”) line 146

Just an anecdote from personal experience and years of headache: Our lab has been trying to apply a specific networks neuroscience approach called "structural covariance networks". We initially applied it to test the local hyperconnection hypothesis in ASD. It took us years to realise and acknowledge that the computational method itself is very problematic in terms of being replicable even in data from the same scanner, site etc., and despite controlling for every biological variable imaginable. It took us another year, and a very talented student, to understand that it is the method itself that enhances the noise in the data in a very "unuseful" way thus drowning any biological effect. We finally could publish this insight here: https://pubmed.ncbi.nlm.nih.gov/32621973/ I use this example to highlight that our "problem" could not really be framed as a hypothesis refuting exercise, as the real insight for us, and I hope also for the community, was not whether the original hypothesis was right or wrong, but that our tool was flawed.

We appreciate the reviewer sharing this illustrative example. It does add a dimension (weak hypothesis v. weak method) that requires recognition in this manuscript. I might additionally argue though that stronger hypothesis (including alternative hypotheses) place the investigator in a better position to detect flawed methodology. That is, truly spurious results may stand-out against sanity checks offered by strong hypotheses, but the point still stands that faulty methods contribute to problems of scientific reliability (something we allude to briefly at the outset with reference to Alipourfard et al., 2021). We now add comment on this on and references to examples for how methods/stats can lead to systematically flawed results (line 238). We now write:

“Strong hypotheses must be matched with methods that can provide clear tests, a coupling that cannot be overstated. In the brain imaging literature alone, there are poignant examples where flawed methods (or misunderstanding of their applications) has resulted in the repeated substantiation of spurious results (in structural covariance analysis see Carmen et al., 2021 and in resting-state fMRI see Satterthwaite et al., 2016; Van Dijk et al., 2012).”

12. The caption for Figure 2 is confusing, and the content of (Priestley et al., under review) is not clear; please delete this figure and add one or two sentences to the text to say that the number of papers in [subject] has increased from about XX per year in 1970 to YYY per year in 2020.

We have accepted this recommendation and have deleted the figure and replaced it with statistics highlighting the annual increase in publication numbers.

Author details

1. Sarah M Rajtmajer

   Sarah M Rajtmajer is in the College of Information Sciences and Technology, The Pennsylvania State University, University Park, United States

   Contribution

   Writing – original draft, Writing – review and editing

   Competing interests

   No competing interests declared

   "This ORCID iD identifies the author of this article:" 0000-0002-1464-0848

2. Timothy M Errington

   Timothy M Errington is at the Center for Open Science, Charlottesville, United States

   Contribution

   Writing – review and editing

   Competing interests

   No competing interests declared

   "This ORCID iD identifies the author of this article:" 0000-0002-4959-5143

3. Frank G Hillary

   Frank G Hillary is in the Department of Psychology and the Social Life and Engineering Sciences Imaging Center, The Pennsylvania State University, University Park, United States

   Contribution

   Conceptualization, Writing – original draft, Writing – review and editing

   For correspondence

   fhillary@psu.edu

   Competing interests

   No competing interests declared

   "This ORCID iD identifies the author of this article:" 0000-0002-1427-0218

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