The National Toxicology Program (NTP) monograph presents a systematic review of animal studies of fluoride exposure related to learning and memory that were published from 2015 to August 20, 2019, as an update of the agency’s 2016 systematic review (NTP 2016). The 2016 review found a low-to-moderate level of evidence that learning and memory deficits occur in experimental animals exposed to fluoride, a finding that prompted NTP to conduct its own study (McPherson et al. 2018). On the basis of its updated systematic review, NTP changed its conclusion to a finding that the animal data are inadequate to inform conclusions on cognitive effects. This chapter reviews the major steps of the systematic review and how it was used to draw hazard-identification conclusions.
In accordance with its protocol, NTP conducted a comprehensive literature search for animal studies of fluoride exposure and measures of learning and memory.1 However, NTP’s inclusion and exclusion criteria for screening the animal literature at the full text level are not documented in either the protocol or the monograph. As noted in Chapter 2, that omission is critical because detailed criteria offer greater clarity for understanding and documenting the process for identifying relevant studies.
A concern for the committee was whether NTP’s risk-of-bias evaluations adequately captured important threats to internal validity that are specific to neurobehavioral outcomes in animal tests. The guidance in the protocol touched on
1 Although the mechanistic evidence is considered separately from the animal evidence, and the committee focused on the animal evidence, the committee questioned whether the literature search strategy for mechanistic evidence was adequate to capture all relevant information, especially with respect to studies that analyzed data derived from new approach methodologies. For example, publications that report testing of large numbers of chemicals in which chemical names are present only in tables or supplemental files might not be captured.
some of the threats, but insufficient detail was provided to ensure a rigorous, consistent evaluation of neurobehavioral studies. Concerns regarding several risk-of-bias domains are discussed below.
Findings of neurotoxicity or neurodevelopmental toxicity of any kind are seriously confounded at doses that result in excessive animal deaths. For example, Kinawy and Al-Eidan (2018)—a study considered by NTP—reported a 30% decrease in the number of offspring in a fluoride-treated group; this result raises serious concerns about the validity of the study’s findings. Given its review of some key studies, the committee is concerned that high mortality was not adequately considered by NTP when it evaluated the animal studies for this risk-of-bias domain.
Confidence in the Outcome Assessment
The protocol lists examples of “well-established methods” for measuring particular outcomes and refers to meeting “standard protocols for each of these well-established methods” for a study to be rated as having a low risk of bias (NTP 2017, p. 65). The committee found, however, several examples of studies in which inappropriate testing procedures were followed or descriptions of methods were insufficient to evaluate their adequacy. That issue indicated to the committee that the risk-of-bias raters simply looked for a test name to determine whether the method was “reliable” without assessing whether methods were suitable to support confidence in the validity of the results. For example, some of the test periods in open-field tests of locomotor activity were too short (3–5 min) to provide reliable, reproducible, or meaningful results (see, for example, Balaji et al. 2015; Bartos et al. 2015; Pereira et al. 2011; Kivrak 2012; Sárközi et al. 2015; Zheng et al. 2016; Nageshwar et al. 2017; Nkpaa and Onyeso 2018; Sun et al. 2018; Wang et al. 2018). All those studies are described by raters as having used acceptable methods. Many published reports indicate that important chemical-related effects on motor activity are detected only after the first 3–5 min of testing (see, for example, Curran et al. 2011; Amos-Kroohs et al. 2015). For that reason, national and international guidance and guidelines for neurotoxicity and developmental-neurotoxicity testing recommend testing with automated systems that have activity sessions of at least 30 min (see, for example, EPA 1998a,b; OECD 2007; NAFTA 2016).
Another concern is that multiple studies provide incomplete descriptions of neurobehavioral test methods (see, for example, Zhu et al. 2017; Sharma et al. 2018; Raju et al. 2019). Behavioral testing methods, including such widely used tests as the Morris water maze (MWM), are not commercially standardized tests. As a result, there are often deviations from published protocols that can alter the sensitivity of the test. Thus, a method can be referred to as the basis of what was
done, but authors still should describe the apparatus, testing conditions, procedures, and dependent measures that they record and note any changes that might affect the reliability and relevance of the study outcomes. Failure to do so is problematic. Expert guidance on the proper conduct of behavioral studies is available (see, for example, EPA 1998c; Cory-Slechta et al. 2001; Tyl et al. 2008; Makris et al. 2009; Vorhees and Makris 2015; Vorhees and Williams 2015; NAFTA Technical Working Group on Pesticides 2016).
Proper procedural controls and controls for motivation variables are critical for obtaining valid behavioral data. For example, the MWM was used in a number of studies to measure spatial learning and memory, and the most common outcome reported was how long it took an animal to find the hidden platform. To interpret the results, data on swim speed, the use of visible platform control trials, or measures independent of swim speed are needed. Their absence is a serious deficiency in studies that rely on the MWM. Studies included in the monograph that were missing one or more of those controls for the MWM include Zheng et al. (2016), Dong et al. (2017), Zhu et al. (2017), Ge et al. (2018a,b), and Yang et al. (2018). Authoritative reviews are available to help NTP to identify test-specific controls whose absence constitutes a serious deficiency (see, for example, EPA 1998c; Cory-Slechta et al. 2001; Tyl et al. 2008; Makris et al. 2009; Vorhees and Makris 2015; Vorhees and Williams 2015; NAFTA Technical Working Group on Pesticides 2016).
The committee identified several problems related to evaluation of statistical analyses in the animal studies. Although failure to control for litter effects was a critical risk-of-bias factor, the monograph does not appear to give this deficiency proper consideration. For example, Chen et al. (2018), Sudhakar et al. (2018a,b), Sudhakar and Reddy (2018), Sun et al. (2018), Wang et al. (2018), and Zhu et al. (2017) provide no control for litter effects, and these studies were not rated as having a high risk of bias. If NTP acquired information from the study authors, that needs to be clearly documented. Lack of control for litter effects constitutes a critical design and statistical problem in data analyses, and the committee emphasizes the importance of this deficiency for evaluating study validity, particularly in studies that include prenatal exposures.
A second problem is that assumptions made in the appraisals about litters, sample size, and statistics appear to go beyond what the authors of the papers specify. For example, if there were five litters per group in a study, and the results indicate that behavioral outcomes were based on five offspring per group, the monograph seems to indicate that because the sample sizes for litter and offspring are the same, the offspring must have come from five different litters. The committee recommends against such assumptions. Unless stated in the paper or confirmed by NTP via direct communication with the authors, it should never be assumed that the number of offspring tested came from unique litters; experience shows that that is generally not the case. A better assumption is that in the absence
of definitive information, the animals did not come from unique litters. Even if offspring came from different litters, if the sex of the offspring is not specified, they could be a mixture of males and females. Males and females exhibit sexually dimorphic behaviors in virtually all behavioral tests, so it is important that results are reported according to sex.
A third problem is that the protocol does not provide sufficient guidance for evaluating statistical analyses. The committee identified a few cases of unacceptable or inappropriate methods, such as the use of multiple t-tests, and inadequate sample sizes. For example, Shalini and Sharma (2015) and Li et al. (2019) used 32 and 45 t-tests, respectively, as the statistical method for identifying group differences, but the Health Assessment Workspace Collaborative (HAWC) appraisal states that the “statistical analyses were reasonable.” The use of multiple t-tests that have not been corrected for multiple comparisons or end points has been widely regarded as inappropriate in neurotoxicity research for decades (Muller et al. 1984). A second example is the inappropriate analysis of learning and memory data by using one-way ANOVA. Learning and memory assays require testing over days, usually with multiple trials per day; thus, at a minimum, a repeated-measures ANOVA is required.
Other Potential Threats to Internal Validity
The committee found a threat to internal validity that was not adequately captured in the risk-of-bias criteria described in the protocol. Evidence of severe toxicity as reflected in excessive body-weight loss or significantly lower body-weight gain in exposed compared to control animals is a serious deficiency in developmental-exposure studies. For example, Mesram et al. (2016) reported about 43% lower body weights and about 20% lower brain weights in fluoride-exposed animals compared to controls during early postnatal development. Shalini and Sharma (2015) reported 10% lower body weights and 7% lower brain weights in a 60-day adult fluoride-exposure study. Several adult- and developmental-neurotoxicity studies failed to measure or failed to report maternal, fetal, or pup toxicity (see, for example, Banala et al. 2018; Sudhakar et al. 2018a). Although severe postnatal toxicity was mentioned in risk-of-bias assessments of some studies, it is unclear whether maternal, fetal, or pup toxicity was routinely assessed in all studies. Such effects can seriously confound interpretation of neurodevelopmental effects, and the committee recommends review of those critical variables in neurodevelopmental studies as part of the risk-of-bias assessment.
Exclusion of Studies
Individual studies are normally excluded at the screening stage but can be excluded later in the process if they have a high risk of bias. As noted by NRC (2014, p. 76), “some studies that entail a substantial risk of bias or that have severe methodologic shortcomings (‘fatal flaws’) [can] be excluded from consideration.
Examples of such exclusion criteria include instability of test compound, inappropriate animal models, inadequate or no controls (or comparison group), or invalid measures of exposure or outcome.” NRC (2014) stated that the exclusion criteria should be described in the protocol.
The committee found that some studies cited in the monograph had severe methodologic shortcomings that could potentially warrant exclusion from the body of evidence that informs conclusions about hazard. The shortcomings include evidence of high mortality or severe toxicity, lack of proper controls, and failure to control for litter effects. NTP should define thresholds or conditions for exclusion; authoritative reviews (see, for example, EPA 1998c; Cory-Slechta et al. 2001; Tyl et al. 2008; Makris et al. 2009; Vorhees and Makris 2015; Vorhees and Williams 2015; NAFTA Technical Working Group on Pesticides 2016) can provide a basis for doing so.
Overall Presentation of Study Ratings
The committee had concerns regarding the presentation of risk of bias in the animal evidence. First, the approach to present the evidence differed among the outcomes being considered. For example, risk-of-bias heatmaps were presented separately for lower risk-of-bias and higher risk-of-bias studies of biochemical, neurotransmission, oxidative stress, and histopathology end points (that is similar to what was done with the epidemiology studies), whereas the studies of learning and memory were not stratified in this way. Criteria for stratifying the studies were not presented, so it was unclear how the various risk-of-bias elements were weighted and it was not stated why the learning and memory studies were not stratified. An explicit description of how studies were stratified according to their risk of bias or a ranking of the animal studies is needed for better communication of how the evaluations of individual risk-of-bias elements were integrated to determine the overall quality of any given study. The committee emphasizes that it is not recommending that studies be stratified but to explain clearly what approach is used to evaluate the evidence.
The committee found that the presentation of the risk-of-bias evaluation suffered from a lack of standard ontology for methods and outcomes (see Hardy et al. 2012 and Baker et al. 2018 for relevant ontologic considerations) among the risk-of-bias evaluations and from a the lack of coherence in descriptors between the summary figures of risk of bias presented in the monograph and those in HAWC. For example, the term open field as a test method of locomotor activity is used to describe studies that used subjective observer ratings and studies that used automated methods. Those types of studies should not be labeled as equivalent. If such an ontology does not exist, it should be reported as a gap in the report.
Several studies (for example, Nageshwar et al. 2017; Nkpaa and Onyeso 2018) involved exposure to fluoride alone and in combination with other treatments, and it was unclear whether NTP evaluated tests of statistical significance appropriately when extracting data from them. That is important because the studies analyzed data collectively, but NTP extracted data only from the control and fluoride-treatment groups, so it was unclear how the effect of fluoride was distinguished from effects in the other treatment groups. A few studies used multiple uncorrected t-tests inappropriately and made all possible comparisons. Did NTP use the t-tests to compare only the control vs the NaF group? How was that done when there were multiple fluoride-dose groups? And what was done when the data were analyzed by ANOVA followed by post hoc individual group comparisons? In those cases, the use of such post hoc tests for a subset of comparisons would not be possible because the error term from the ANOVA includes error variance from all groups, including ones that involved other treatment combinations. A large proportion of the fluoride studies had one to four additional groups exposed to fluoride and a hypothesized “protective” substance; this makes separating fluoride effects from controls difficult or impossible without access to the raw data for reanalyzing the data relevant to the systematic review. The monograph does not describe how that important problem was handled.
One consideration in assessing the body of the evidence is sample size, which is critical in neurotoxicity studies.2 The use of small samples undermines the basis of sampling theory; as sample size decreases, the probability of type II errors increases. For example, the Manusha et al. (2019) study used only five animals per treatment group, and Chen et al. (2018) only six. The evaluation does not mention the very small groups, whose use leads to low study power and difficulties in replication because of large standard errors. The committee was surprised that sample size was apparently not considered as part of NTP’s evaluation given that national and international neurotoxicity guidance and guidelines require sample sizes of at least 10 males and females per treatment group (see, for example, EPA 1998a,b).
2 Several committee members felt that sample size should be considered as a risk-of-bias element, and individual studies possibly excluded because they used very small samples, but they recognized that that approach is not consistent with current systematic-review methods.
On the basis of the information provided in the monograph, it was not obvious to the committee whether NTP followed the protocol to reach its conclusions about the animal evidence. There was no explicit discussion of NTP’s confidence in the body of evidence. Rather NTP dismissed all the animal studies by stating that collectively they are “inadequate to inform conclusions on whether fluoride exposure is associated with cognitive effects…in humans” (NTP 2019, p. 2). That conclusion is based on the contention that it is not possible to separate effects on cognitive end points from effects on locomotor activity or motor coordination. In other words, the entire animal dataset on fluoride is essentially dismissed from consideration because changes in locomotor activity in fluoride-exposed animals were regarded as confounding the interpretation of all learning and memory data. The committee questions that rationale. Locomotor-activity changes can sometimes affect learning and memory outcomes, but often they do not, and given that many of the fluoride studies used 3- to 5-min open-field tests that are unreliable measures of locomotor activity, it is inappropriate to use differences in such tenuous assessments to exclude learning and memory results. Moreover, it has been demonstrated many times that the presumed confounding influence of activity on learning and memory behavior does not occur. For example, open-field activity changes do not necessarily translate to swimming tasks. Hence, MWM studies are unlikely to be affected by open-field activity differences unless the activity changes are large and persistent, and this cannot be determined from 3- to 5-min tests of exploration. Even if it could be determined, it must be shown that such locomotor effects are present in a measure, such as swim speed, that directly affects performance in the learning and memory part of the task. If swim speeds are comparable among groups, locomotor-activity differences are not a concern for MWM outcomes. Moreover, swim speed does not affect some dependent measures in the MWM, such as path length and path efficiency. For example, the Yang et al. (2018) study found no effect of fluoride on swimming path length in the MWM—a measure of learning—a result that indicates that any changes found in the 3-min open-field test did not confound findings related to cognition. In the fluoride-neurotoxicity literature, more careful analyses are largely absent, and it is a mistake to dismiss studies of learning and memory because of minor, brief locomotor activity effects or when other assessments can rule out locomotor confounding effects in cognitive assessments.
The committee found that some studies had serious deficiencies that made it question the protocol guidance for rating the internal validity of the studies. Several of the risk-of-bias elements appear to need more detail to ensure a rigorous, consistent evaluation of the neurobehavioral studies, and NTP should consider excluding studies that have specific egregious deficiencies (high mortality or severe toxicity, lack of proper controls, and failure to control for litter effects).
The committee also questions NTP’s rationale for dismissing the animal evidence as discussed above. Given the serious concerns raised by the committee, NTP will need to decide whether it should reanalyze the animal evidence. The committee cautions, however, that given the poor quality of the animal studies that it reviewed, revising the systematic review to address the concerns highlighted might not affect the finding that the animal evidence is inadequate to inform conclusions about fluoride exposure and neurodevelopmental and cognitive effects in humans.
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