「降级」损失的是两笔账:范围损失加样本也补不回,功效损失加点样本就回来

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Evidence level: C

一个参数被降级,效应量没变小,变小的是这句话能盖住的范围——而范围不是靠加样本能买回来的。

一、降级没让效应变小,只让「能对谁说」变窄

一个参数从跨设备合并降级为单设备内比较,效应量本身丝毫未动:同一批人、同一台机器、同一个差值。变的是这句话能盖住谁。前者敢说「在这类人身上成立」,后者只能退到「这台设备上、这批人里成立」。

这两件事在统计上不同源。精度是随机误差问题,靠样本量收窄;范围是系统误差问题,靠改变设计。把它们合成一个「损失」再来比大小,等于把两把不同刻度的尺子叠在同一张表上。

所以第一件事是把账分开记。功效损失问「还测不测得出来」,范围损失问「测出来的对谁算数」。

二、功效损失的分母是标准误,加样本就回来

固定总样本,比较两种方案的功效:单设备内比较只用人不重叠的那一截,跨设备合并用全部人但吃进设备偏倚。偏倚小时,合并的 n 更大、标准误更小,功效反而更高;偏倚一大,偏倚转成的方差就把 n 的收益吃掉。

多中心设计的做法与此同构:中心数与每中心样本量的平衡直接决定功效,最优配比依赖未知的方差参数,于是只能按最坏参数情形保功效(PMID 42479089)。这说明功效损失是可算的,而算法里 n 是自变量。

可算即意味着可补。这条线上加样本有明确回报,回报率是 1/√n。

三、范围损失的分母是人,加样本一点不动它

哮喘那项最直白:社区随机抽样 749 人、179 名现患哮喘,按 GINA 引用的 17 个主要 RCT 入选标准去套,中位仅 4%(0–36%)符合;在接受治疗者中也只有中位 6%(PMID 17105779)。COPD 队列 1309 人套 16 个试验,符合率 2.3%–46.7%,剔除最狠的三条是 FEV1(39.9%)、上年急性加重次数(36.7%)、吸烟史(16.8%)(PMID 31299936)。

这个比例的分子分母都与样本量无关。把它放大十倍,4% 还是 4%。因此「加样本到 4 倍」对范围损失的作用精确为零——不是收效甚微,是结构上无效。

四、更麻烦的是:降范围可能顺手升功效

癌症预防试验的老争论提供了关键结构:为提功效只招高危人群,前提是「相对风险在各风险层保持不变」。若真实情形是「绝对风险差不变」,高危人群试验的功效反而可能更低;同时利益/危害比在高危者身上更好看,直接外推到一般人群就是误导(PMID 15461821)。

这一条把两笔账的关系讲透了:它们不是同一根轴的两端,可以一个升一个降。于是「降级是否过度保守」没有统一答案,只能对具体参数、具体设备对、具体目标人群各算一次。

五、平台期在哪:连异质性有多大都没测准

功效曲线会拐平。拐平的原因不是样本不够,是限制因素换了人——从随机误差换成异质性与中心数。小中心数、入组严重失衡时渐近正态近似失效,p 值不可靠,标准近似漏掉真实风险因素,直接制造 II 类错误(PMID 41569702)。

更麻烦的是「异质性有多大」本身就估不准:7 项研究、真实异质性 80% 时,I² 平均低估 28 个百分点;真实无异质性时又高估 12 个百分点(PMID 25880989)。平台期的位置正依赖这个被系统性低估的量。

所以「要加到几倍样本」这个界,不能由单点 I² 反解。该报的是预测区间——将来类似场景的真效应可能落在哪(PMID 27406637)。

六、范围损失还有一层:参加试验本身就是个效应

把结果搬到日常场景,隐含假设是「参加试验这件事不改变结局」。这个假设常常不成立。Ung 等人把试验参与效应写成正式估计量:只有在「参与×治疗」无交互时,才能用试验数据叠加目标人群的协变量分布,识别出日常照护下的平均效应(PMID 40266689)。

补救方向是有的:后分层与 g 方法(逆概率加权、标准化)在假设层面一一对应,可以用目标人群的年龄性别分布把估计加权过去(PMID 41992116)。但前提是那些协变量测到了,且效应修饰结构猜对了。

现实是:456 个肿瘤 RCT 里仅 51.8% 报了筛查人数,仅 21.5% 讨论了可推广性(PMID 36826121)。做范围损失估计的原料,一半以上根本没记。

七、反转:这不是「二选一」,是两种不同的研究

把降级重新命名,问题就消解了:单设备内比较是一种窄口径设计(内部有效度优先、可加样本),跨设备合并是一种宽口径设计(覆盖更广、但设备被降格为效应修饰因子)。它们不是同一个估计的优等版与劣等版。

正解是分层报告:先报窄口径的精度(效应量 + 可检出差异 + 重复次数),再报「从窄口径推到宽口径还缺哪些协变量、缺了会偏多少」。加样本只在第一层有效,第二层只能靠补测与设计。

四格判据:偏倚 ≥1 倍效应量、加样本 4 倍仍补不回 → 改判范围损失,设计改为分层报告;偏倚 ≤0.5 倍且功效差 <10%、覆盖缺口 <15% → 降级属过度保守,应保留合并;功效出现平台期 → 该点即「补不回」的上界,须写入方案;模拟与实测的范围损失差 >2 倍 → 范围损失只能实测标定,不许由模拟外推。

证据与局限

已验证: 主要 RCT 的入选标准只覆盖真实患病人群的极小部分——哮喘中位 4%(0–36%)(PMID 17105779)、COPD 2.3%–46.7%(PMID 31299936);只招高危人群并不必然提高功效,取决于不变的是相对风险还是绝对风险差(PMID 15461821);大样本量会带来统计显著而临床不相关的效应,超需样本的试验中 72% 报显著、仅 15% 具临床相关性(PMID 32153391);小样本 meta 分析中 I² 存在 12–28 个百分点的系统偏倚(PMID 25880989);小中心数或入组失衡时渐近近似失效,可致 II 类错误(PMID 41569702);试验参与效应会破坏结果外推,仅在无交互假设下可识别(PMID 40266689);后分层与 g 方法假设可对应,可用目标人群协变量分布加权(PMID 41992116);多中心设计的功效同时取决于中心数与每中心样本量(PMID 42479089);预测区间比 τ²/I² 更便于临床解读(PMID 27406637);肿瘤 RCT 中仅 51.8% 报告筛查人数、21.5% 讨论可推广性(PMID 36826121)。

部分验证: 上述证据全部来自临床研究与统计方法学,没有一条是在丹田呼吸参数上做的。「范围损失 vs 功效损失」的二分在方法学上成立,但两个量在丹田参数上的具体数值、以及偏倚/效应量比值落在哪一档,均无实测。降级阈值 0.5 倍与 1 倍效应量是本文设定的判据,不是文献结论。

待验证: ①丹田五参数在偏倚 0/0.5/1 倍效应量三档下的功效差(功效损失)从未算过;②单设备内 vs 跨设备合并两方案在参数真值空间中「结论仍成立」的比例(范围损失)无实测标定;③样本量-功效曲线的平台期位置在五参数上完全未知;④模拟与实测的范围损失量级差是否真的 >2 倍,须实测才知道;⑤本项目的目标人群(修炼者与新手)协变量分布从未刻画,后分层加权缺原料。

L1 网络状态:该主题尚未进入 L1 对应网络。原文节点表按三类域分派 ——「| 节点 | 各域的概念/量(五行、五脏、频率、颜色…) | 按域分派(见下表) |」,即易学/中医侧、物理侧、生理/体验侧,无「测量学」维度节点(无范围损失、功效损失、外部效度、目标人群、效应修饰分布);边表止于 E-050(六十甲子纳音→60 个频率,状态 open),无任何以测量规则、筛选阈值或可推广性为源或目标的边。

相关阅读

证据等级: C
参考文献: PMID 17105779, PMID 31299936, PMID 15461821, PMID 32153391, PMID 25880989, PMID 41569702, PMID 40266689, PMID 41992116, PMID 42479089, PMID 27406637, PMID 36826121


免责说明:本文属传统知识与科学文献的整理、对照与研究设计讨论,仅供理解与参考,不构成医疗建议,不能替代专业诊断与治疗。文中涉及的效应量、频率区间与暴露结论多为研究报告层面的推断,个体情况差异很大;如有身体不适或健康疑虑,请就医并由专业医师判断。

The Costs of Downgrading: Range Loss and Irrecoverable Sample Loss vs. Efficiency Loss Recoverable with More Samples

Evidence level: C

When a parameter is downgraded, the effect size does not shrink; what shrinks is the scope over which this statement holds—and scope cannot be purchased by adding samples.

I. Downgrading Does Not Shrink Effect Size; It Narrows “Who It Applies To”

When a parameter is downgraded from cross-device merging to within-device comparison, the effect size itself remains unchanged: the same subjects, the same machine, the same difference. What changes is the scope of applicability. The former can confidently claim validity for “this type of person”; the latter retreats to validity only “on this device, within this cohort.”

These two aspects are statistically distinct. Precision is a random error issue addressed by sample size; scope is a systematic error issue addressed by design change. Combining them into a single “loss” for comparison is like stacking rulers with different scales on the same table.

Therefore, the accounts must be kept separate. Effectiveness loss asks “Can we still detect it?” Scope loss asks “For whom does the detection count?”

II. The Denominator for Effectiveness Loss is Standard Error; Adding Samples Restores It

With a fixed total sample size, comparing the two designs: within-device comparison uses only the non-overlapping portion of participants, while cross-device merging uses all participants but absorbs device bias. When bias is small, the merged design has a larger $n$ and smaller standard error, yielding higher power. However, when bias is large, the variance converted from bias consumes $n$’s benefit.

This mirrors multi-center designs: the balance between center count and sample size per center directly determines power. Optimal allocation depends on unknown variance parameters, necessitating power preservation under worst-case parameter scenarios (PMID 42479089). This demonstrates that effectiveness loss is calculable, and $n$ is an independent variable in the algorithm.

Calculability implies reparability. Along this line, adding samples yields a clear return, with a rate of $1/\sqrt{n}$.

III. The Denominator for Scope Loss is People; Adding Samples Does Not Change It

The asthma example is most direct: community random sampling of 749 people, with 179 having current asthma. Applying inclusion criteria from the 17 major RCTs cited by GINA yielded a median fit rate of only 4% (0–36%). Among treated individuals, the median was also 6% (PMID 17105779). In a COPD cohort of 1309 people applying 16 trials, fit rates ranged from 2.3% to 46.7%; removing the three most stringent criteria (FEV1 at 39.9%, prior exacerbations at 36.7%, smoking history at 16.8%) still left significant gaps (PMID 31299936).

The numerator and denominator of this proportion are independent of sample size. Scaling it tenfold leaves 4% as 4%. Therefore, “adding samples to four times the original” has a precise effect of zero on scope loss—not marginal gain, but structurally invalid.

IV. A Complication: Reducing Scope May Incidentally Increase Effectiveness

The longstanding debate in cancer prevention trials provides key structural insight: to increase power, recruiting only high-risk populations assumes “relative risk remains constant across risk strata.” If the reality is “absolute risk difference remains constant,” power in high-risk populations may actually be lower; meanwhile, the benefit/harm ratio looks better for high-risk individuals. Directly extrapolating to the general population becomes misleading (PMID 15461821).

This clarifies the relationship between the two accounts: they are not endpoints on the same axis; one can increase while the other decreases. Thus, “whether downgrading is overly conservative” has no unified answer; it must be calculated once for each specific parameter, device pair, and target population.

V. Where the Plateau Lies: Even Heterogeneity Magnitude Is Not Measured Accurately

Power curves flatten. The flattening is not due to insufficient sample size but a shift in limiting factors—from random error to heterogeneity and center count. With small center counts or severe enrollment imbalance, asymptotic normal approximations fail; p-values become unreliable, and standard approximations miss true risk factors, directly generating Type II errors (PMID 41569702).

More problematic is the inaccuracy in estimating “how large the heterogeneity is”: with 7 studies and true heterogeneity at 80%, $I^2$ underestimates by an average of 28 percentage points; with no true heterogeneity, it overestimates by 12 percentage points (PMID 25880989). The position of the plateau depends precisely on this systematically underestimated quantity.

Therefore, the threshold “how many times to add samples” cannot be reverse-solved from a single-point $I^2$. Instead, one should report prediction intervals—where the true effect in similar future scenarios may fall (PMID 27406637).

VI. Another Layer of Scope Loss: Participation in the Trial Is Itself an Effect

Moving results to real-world settings implicitly assumes “participating in the trial does not change the outcome.” This assumption often fails. Ung et al. formalized the participation effect as an estimator: only under the assumption of no interaction between “participation × treatment” can trial data be combined with target population covariate distributions to identify average effects under routine care (PMID 40266689).

Remedial directions exist: post-stratification and g-methods (inverse probability weighting, standardization) correspond one-to-one at the assumption level; estimates can be weighted back to the target population’s age and gender distribution (PMID 41992116). However, this requires that those covariates were measured and the effect modification structure is correctly guessed.

Reality: Among 456 tumor RCTs, only 51.8% reported screening numbers, and only 21.5% discussed generalizability (PMID 36826121). Raw materials for estimating scope loss are missing in over half the cases.

VII. Reversal: This Is Not “Either/Or,” But Two Different Types of Studies

Renaming the downgrade resolves the problem: within-device comparison is a narrow-caliber design (prioritizing internal validity, allowing sample addition), while cross-device merging is a broad-caliber design (covering wider scope but downgrading the device as an effect modifier). They are not a superior and inferior version of the same estimate.

The correct approach is stratified reporting: first report precision of the narrow caliber (effect size, detectable difference, replication count), then report “what covariates are missing to extrapolate from narrow to broad caliber, and how much bias would result.” Adding samples is only effective at the first layer; the second layer requires additional measurement and design.

Four-Grid Judgment Criteria:
* Bias $\ge$ 1x effect size AND adding 4x samples still fails to recover $\rightarrow$ Classify as Scope Loss; redesign for stratified reporting.
* Bias $\le$ 0.5x effect size AND power loss <10% AND coverage gap <15% $\rightarrow$ Downgrading is overly conservative; retain merging.
* Power plateau appears $\rightarrow$ This point is the upper bound of “unrecoverable”; must be written into the protocol.
* Difference between simulated and measured scope loss >2x $\rightarrow$ Scope loss can only be calibrated via measurement; extrapolation from simulation is prohibited.

Evidence and Limitations

Verified: Inclusion criteria for major RCTs cover only a tiny fraction of the true diseased population—median 4% (0–36%) in asthma (PMID 17105779), 2.3%–46.7% in COPD (PMID 31299936); recruiting only high-risk populations does not necessarily increase power, depending on whether relative risk or absolute risk difference remains invariant (PMID 15461821); large sample sizes yield statistically significant but clinically irrelevant effects; in trials with excessive samples, 72% report significance while only 15% show clinical relevance (PMID 32153391); $I^2$ exhibits systematic bias of 12–28 percentage points in small-sample meta-analyses (PMID 25880989); asymptotic approximations fail with small center counts or enrollment imbalance, potentially causing Type II errors (PMID 41569702); trial participation effects disrupt extrapolation, identifiable only under no-interaction assumptions (PMID 40266689); post-stratification and g-methods assumptions correspond, allowing weighting by target population covariate distributions (PMID 41992116); power in multi-center designs depends simultaneously on center count and sample size per center (PMID 42479089); prediction intervals are more clinically interpretable than $\tau^2/I^2$ (PMID 27406637); only 51.8% of tumor RCTs reported screening numbers and 21.5% discussed generalizability (PMID 36826121).

Partially Verified: All evidence above comes from clinical research and statistical methodology; no study was conducted on Dantian breathing parameters. The binary distinction between “Scope Loss vs. Effectiveness Loss” holds methodologically, but specific numerical values for these quantities in Dantian parameters, and which tier the bias/effect size ratio falls into, lack empirical calibration. The downgrade thresholds of 0.5x and 1x effect size are criteria set in this paper, not conclusions from literature.

To Be Verified: ① The difference in power across three tiers of bias (0/0.5/1x effect size) for the five Dantian parameters (effectiveness loss) has never been calculated; ② The proportion where “conclusions remain valid” in the parameter truth space for both within-device and cross-device designs (scope loss) lacks empirical calibration; ③ The position of the plateau on the sample size-power curve is completely unknown for the five parameters; ④ Whether the magnitude difference between simulated and measured scope loss truly exceeds 2x requires empirical verification; ⑤ The covariate distribution of this project’s target population (practitioners vs. novices) has never been characterized, leaving raw materials for post-stratification weighting missing.

L1 Network Status: This topic has not yet entered the L1 corresponding network. Original node tables are distributed across three domains—”| Node | Concepts/Quantities per Domain (Five Phases, Five Organs, Frequencies, Colors…) | Distribution by Domain (see table below) |”, i.e., Yijing/TCM side, Physics side, Physiological/Experiential side, with no “Measurement Science” dimension nodes (no scope loss, effectiveness loss, external validity, target population, effect modification distribution); edge tables end at E-050 (60 Na Yin $\rightarrow$ 60 frequencies, status open), with no edges sourced or targeted by measurement rules, screening thresholds, or generalizability.

Related Reading

Evidence Level: C
References: PMID 17105779, PMID 31299936, PMID 15461821, PMID 32153391, PMID 25880989, PMID 41569702, PMID 40266689, PMID 41992116, PMID 42479089, PMID 27406637, PMID 36826121


Disclaimer: This article compiles traditional knowledge and scientific literature for comparison and research-design discussion only. It is not medical advice and cannot replace professional diagnosis or treatment. Effect sizes, frequency ranges and exposure conclusions cited here are largely inferences at the research-report level, and individual circumstances vary widely. If you have any discomfort or health concerns, please consult a physician.

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